General comments

This study uses the CHASER chemistry model, along with a number of observational products of lightning and atmospheric chemicals from aircraft and satellites. A number of lightning parametrisations were implemented and compared. The study concludes that several lightning schemes reduced certain biases when compared to the often-used, cloud-top height lightning scheme. 20-year trends were also compared, both with and without nudging to reanalysis meteorology. The show a wide range of trends from negative trends to some that are much higher than found with the cloud-top height lightning scheme.

Overall the paper is well written. It provides a useful demonstration of these different lightning schemes, and explores to a high level of detail how they interact with atmospheric chemistry. Notably, considering how trends in lightning NOx emissions impact trends in column NOx and ozone. There are a few general points that I think need addressed before it is suitable for publication:

1. The lightning observations compared to are not for the same time period. I appreciate this is to try and look at near-global observations, but I propose below suitable sensitivity analysis to assess the uncertainty introduced by the inconsistency in time period.
2. Whilst differences in correlations/stats can be, and are, described, you should acknowledge where these differences are sufficiently small that they may not be real (e.g. correlations within a few 0.01s of each other). Assess whether it is appropriate to draw conclusions from differences of this magnitude, especially given uncertainties in observations (even if you were using the same time period).
3. The modelled results are actually fairly similar in many cases, as such it should be acknowledged that the input variables for some (e.g. cloud-top height) might be better observed and with a better understood response to climate change, than others (e.g. cloud ice). As this may be a more important factor for some modellers, than the small differences in bias found here.

Specific major comments

L23/section3.4. I don’t agree that you can call this “long-term” trend analysis. 20 years is considered to be on the scale of internal variability of climate, and not even as long as the normal averaging period for looking at trends, let alone looking at the trend within that time period. I think it is helpful to show the trends but I would be more refrained in how you describe them. they may indicate the response to warming but cannot be assumed to be the same as the climate response. I would avoid saying “under global warming” and instead say it could be a “short-term response to surface warming” since if there is anything other than decadal variability in the signal, then it is the transient climate response not the equilibrium response. You should note this if you are comparing to other estimates, because they may be looking at the equilibrium response.

L128. I’m not sure where is best to acknowledge it, but I think you need to highlight the issues around using a constant isobar for climate change simulations. As much as it is not an issue for your simulation necessarily, you are trying to relate your results to climate change and if there is significant climate change the same isobar may not be appropriate. In Finney (2018) a different isobar was used for 2100 RCP8.5. A potentially neater solution is to use an isotherm as proposed by Romps (2019). If you have tried this it would be good to include what you found, but if not I think it would be helpful to at least acknowledge the isotherm-alternative as a more flexible approach to applying the ICEFLUX parametrisation.

L245. Whilst I think it is of interest to have compared to OTD, it is a completely different 5 year period. It is quite possible that interdecadal/annual variability would influence results. I strongly recommend checking this by reproducing results within +-45degrees. For this domain you can compare against LIS for the same years, and then against OTD just in that domain. The difference in the statistics compared against OTD, opposed to LIS, will show you how much error may be in your +-75 degree statistics. Alternatively, is there not a full LIS/OTD climatology product, which would mean at least you were using a good number of years (>10years) for the tropics climatology.

Fig14. If both green and red lines use the same LNOx emissions in 2001, how can they have different column NOx in 2001? What is the differences between the models? Spinup? This is particularly concerning in panel h. You need explain these lines begin, and even end up offset, whilst the other panels don’t.

North Pacific analysis. I can’t see that this is particularly interesting. I would remove. Whilst there are some notable trends in the north pacific, the absolute amount of LNOx emission is small so it’s unlikely to have a major effect on column NOx and O3 in this region. As indeed you have found. Your own fig7 shows that none of the schemes result in a big effect from lightning on column NO2 in the north pacific.

L597. I don’t think you can use a review from 2008 (or 2009 in the bibliography!) to say what recent estimates say are expected. Recent estimates (within the last decade of studies) are highly conflicting, and it’s hard to say that any particular trend can be expected. You could say the majority of estimates show a positive trend, and tend average close to 10%/degree, but I would struggle to see a justification for anything stronger.

Specific minor comments

L11. “, also” to “is based on X, and has been…” At the moment it sounds like ICEFLUX is also in ECMWF model but I don’t believe that’s what you mean. And you need to say what the underlying input variables of the ECMWF parametrisation are

L19. “observations” of what?

L30. “the reproductivity of long-term trends of lightning” to “trends of lightning over longer time periods” or something similar

Introduction. I think somewhere (intro or discussion section maybe) it needs to be acknowledged that whilst ice-based parametrisations are appealing they have greater uncertainty associated with inputs, especially with regard to the microsphyics scheme used. This paper can provide a good basis for that https://agupubs.onlinelibrary.wiley.com/doi/full/10.1029/2021JD035461?casa_token=XPjZ7-BBFZEAAAAA%3AfbdQYuwknvDDXqNO5TJGvAEiUNFpzLMnbt2VnnKcHMC4QXtaq1hUzOs3-PYNAOZvSowW3J3vLuvB

L50. I think it would be worth referencing this paper, regarding what chemistry models are currently doing. It is much more up to date (though no updates to lightning schemes) and it includes some nice looks at the chemistry/radiative impacts of lightning in models. https://acp.copernicus.org/articles/21/1105/2021/

L57. As in abstract you don’t say what the input variables are for the lopez scheme.

L76. A decrease for convective mass flux scheme was also found for CMAM model in Finney (2016a). Not necessary to include but would demonstrate it wasn’t only one model in which this has been seen.

L72. You refer to a USA specific result but actually the tropics is where the dominant LNOx production occurs. The following paper considers a cloud ice based parametrisation for lightning of Africa and finds a relatively small response of lightning to climate change over the continent https://agupubs.onlinelibrary.wiley.com/doi/full/10.1029/2020GL088163

L139. I don’t see that Q_R is a “flux” as there’s not per second in there. Please include the units. I think its kg^2/kgm^2? A bit unusual so not sure how to describe it. You might almost have a flux with Q_R*sqrt(CAPE) as the sqrt of CAPE has units of m/s. But still not sure it works out so I suggest coming up with more precise terminology for what Q_R is.

L140. Can you give a reason for the “1.8” in the min function? What are the units of that? Km?

L170. Eq13 is quite different to Eq8, and changes the meaning of this variable quite a bit. For the better potentially – I can at least see the logic behind it more clearly. I’m not sure I’d call this a modification of the ECMWF param, I’d say it’s probably different enough to have its own identity.

Table 1. Please review your use of “frozen precipitation convective flux”. I do not think it makes sense. Stick to the variables present in the main equation for the parametrisation. ECMWF-mod (Eq 11/12) is based on column precipitating ice and CAPE so I think you should only have two bullet points. I also don’t think it’s a appropriate term for the ECMWF-original inputs but as per L139 comment I’m not really sure what you’d call that.

L186. What is the C-shaped scheme, Pickering et al.? reference?

Table 2. Are experiments 3-6 actually different to experiment 3 or have you just selected out the relevant years? If they are different you need to say how, if not then it seems overkill to call them separate experiements.

Section 2.3.2. I presume you have sampled the specific flight track and timings from the modelled data, for comparison to observations? Can you explicitly state that.

L238. “profile as per Ott(2010)”. Add reference and suggest just get rid of L186-190 which is confusing as it sounded like you were suggesting you’d explored both profiles. If you have then it would be good to know what you found.

Fig3. Showing separate diagrams for full global, ocean-only and land-only could draw out your points about the differences. All schemes, currently lie quite close to each other.

L365. Is this model bias the total global model bias? Or just over the regions in fig9? Is it on an annual or monthly basis?

L370-379 and L548. The differences between these correlation coefficients are generally quite small, and the differences probably not significant. I would go easy on firm conclusions here and at least acknowledge that the correlations are actually very similar (this is something you should consider throughout when referring to differences in correlations).

L437. The majority of these references are looking at the equilibrium response to warming. Clark had a transient simulation but I suspect averaged over a number of decades to show the trend. You are looking at variations over a much smaller timescale. It is interesting to see, but it is comparing apples with oranges to directly compare these. You should acknowledge that they are measuring different kinds of response, over different timescales. You would be better going back to the Williams paper that looks at temperature response on shorter timescales, and relating your results to that… https://ui.adsabs.harvard.edu/abs/2005AtmRe..76..272W/abstract

Fig12. Worth noting in caption why ICEFLUX doesn’t have shading towards the poles?

Technical corrections

L9. “improve” to “improving”

L65. “CPAE” to “CAPE”

Fig6, table3. Say clearly in the caption that these are looking at NO. Currently it doesn’t state.

Fig 10. State in the caption that these are relative to the CTH simulation.

Fig11. Please say what the black blue and red lines are in the caption.

Fig14. Is this accessible to people with red green colour blindness?

Four lightning NO_x production schemes were investigated in the CHASER (MIROC) chemistry climate model: ICEFLUX scheme, the original and modified ECMWF schemes, and the CTH scheme (native to the CHASER model). The model performance was evaluated using OTD (lightning flashes), ATOM (air composition), TROPOMI (NO2 and O3 columns). As the most abundant NOx sources in the mid to upper troposphere, it is important to include LNO_x in global models by implementing and testing LNO_x production schemes. The manuscript is generally well written and clearly presented, but some important pieces were missing or not properly addressed. A major revision is needed before it can be published in GMD for the following reasons:

1. In half of the simulations, the global LNO_x emissions were adjusted to 5.0 TgN/yr using different adjustment factors, but no descriptions were given regarding what are the adjustment factors and how was it done? A detailed description is necessary to understand the process.
2. The NO emissions per flash were set to 111 moles NO per IC (intro-cloud lightning flash) and 1113 moles NO per CG (cloud-to-ground lightning flash) as parameters drawn from work reported by Price et al. (1997). These values were quite outdated, and there are many publications to update the lightning production efficiency (PE) in recent years. And the number 1113 is considered the upper limit of the reported values and is not realistic. In recent years, the commonly recommended values for CG flashes are in the range of 150-350. Please justify your use of these numbers. At the very least, please discuss the uncertainties that may be caused by using different PE values.
3. In the validation of the lightning schemes, the 1996-2000 OTD climatological data was used to compare with the simulations during 2007-2011. As a qualitative measure, it is  probably okay to use the climatological data for a broad range comparison even though the time periods were completely separated. However, since the LIS data was available for the simulation years, albeit it was in a narrower latitude range, it should be used to evaluate the model’s performance.
4. In recent versions of the TROPOMI NO2 column data (http://www.tropomi.eu/data-products/nitrogen-dioxide), there is increase of the tropospheric NO2 columns under some weather conditions. Please provide the detailed version (and level) information of TROPOMI data used in this research and discuss potential uncertainties associated with it.
5. The Taylor diagram showing the prediction accuracy of the various lightning schemes doesn’t seem to present any significant differences among the schemes. With mean values across the globe and spanning so many years, correlation coefficients of 0.80 and 0.79 probably don’t mean much difference. Please provide the significant test and, if possible, a confidential interval would help.
6. I would suggest replacing Figures 4 and 5 using LIS data with the same period as your simulation years. The peaks (most lightning occurrences) appeared between +38° and -38° latitude that the LIS had coverage anyway.
7. The trend analyses for lightning density (Section 3.4) and NO_x and O₃ columns (Section 3.5) were only based on simulation results and compared to the CTH lightning scheme. Because no observational basis, all the analysis is hypothetical and there is no way to know which scheme or schemes could reproduce (or even close to) the truth. Understandably limitation exists in time and space to employ observation-based analysis, but it is still helpful if limited analysis based on observations could be done. For example, for the lightning trend, the LIS/OTD satellite data could be used from the years when the data was available to derive the climatological trend coupled with the trend of temperature during the period. While for NO₂ and O₃ columns, the OMI/TROPOMI data could be employed to examine the trend over the years.

Specific Comments:

1. Page 1 Line 8 and other places, “the most dominant NOx source in the upper troposphere”, I would say mid to upper troposphere.
2. Page 2, Lines 40-47, not only in global models, the studies of LNO_x in regional scale models have also made significant progress in recent years (e.g. Kang et al. 2019:  https://doi.org/10.5194/gmd-12-3071-2019 and https://doi.org/10.5194/gmd-12-4409-2019 and 2020: https://www.nature.com/articles/s41612-020-0108-2), please update the knowledge with references in the discussion.
3. Page 2, Lines 51-55, “However, some new … against the LIS/OTD lightning observations”. These two sentences are basically stating the same thing, please combine and simplify these sentences.
4. Page 2, Lines 57-58, “The two new lightning schemes …”, please provide references.
5. Page 2, Line 58, “The new lightning schemes must be validated …”, the expression “must be” is too strong, consider rewording.
6. Page 19, end of Figure 14 caption, the "without nudging" used twice. One of them should be "with nudging".
7. Page 21, Line 543 and other locations, “Two new lightning schemes”. I would say Three new lightning schemes: the ICEFLUX, two ECMWF schemes (original and modified). It would be more straightforward to me to just say 3 new schemes.
8. One comment on the ICEFLUX as it displayed the downward trend of lightning flashes with rising temperature. Since the rising temperature would mean less ICE and less ICE FLUX, that would result in fewer lightning flashes. This probably suggests the intrinsic shortcomings for this scheme to simulate climate lightning trends.

Review of “Introducing new lightning schemes into the CHASER (MIROC) chemistry climate model” by Yangfeng He et al.

General Comments

This paper presents an interesting set of model experiments that tests different representations of lightning. Unfortunately it is rather unclearly written and many important details are missing, so I have struggled to fully assess its contents. Some of this lack of clarity and missing details are listed below in the Specific Comments section. For example, it is unclear what the un-nudged simulations represent, and it is hence difficult to interpret what is meant by the difference between the nudged and un-nudged runs (and these differences are large). Other aspects of the experiments are also not very clear – e.g., how is soil NOx, the other major natural NOx source, handled? Presumably it is somehow fixed. It is also unclear how the other major NOx emissions (anthropogenic and biomass burning) are prescribed in the experiments. Some of the units are incorrect or unclear. There is little detail about how the TROPOMI comparison is carried out, and I am unsure from what is written if averaging kernels have been applied correctly, to make this a valid evaluation. I appreciate this is mainly a paper that describes the lightning schemes and their differences, but it would be nice to include a bit more discussion on the interpretation of the differences, particularly as they appear to lead to very different trends in lightning.  If all these points can be clarified in a revised version, then this paper may be acceptable for GMD, but in its current form it is not.

Specific Comments

L8 most dominant -> dominant

L11-12 Sentence does not make sense

L19 Biases for what?

L27 Why does nudging make such a large impact on the trends? What do the un-nudged runs represent?

L27 Was the earlier study also 2001-2020 changes?

L30 reproducibility?

L35 Is there such a thing as unreactive NO?

L37 Finney et al (also l53)

L57 The schemes are not ‘described above’

L57 I much prefer evaluated to “validated”

L66 CAPE – also clarify “CAPE x precipitation as a proxy”

L72 Contiguous?

L86 “This study” is ambiguous

L91 (etc) Capitalise Section references

L118 What about other natural NOx sources, e.g. soil?

L132 over land and ocean

L133 Check units

L135 Why was 440 hPa chosen?

L139 In the ECMWF scheme, why is no level specified for the frozen precipitation flux? Surely it varies hugely with vertical level?

L141 The units are a bit confusing (km, day); I suggest standardize on base SI units for all equations.

L142 Is alpha dimensionless?

L163-167 These alphas are not dimensionless and must have odd units that depend on the units used for CAPE.

L172 z0 and z-25 already defined

L185 Definition of D is ambiguous (above 0C – do you mean positive temperatures or at altitudes greater than the 0C isotherm?)

L197 Capitalize Earth

L211 Clarify why you only use a subset of the ATom data.

L236 Table 2 could give more details of each experiment. E.g., are HTAP2 (2008) anthropogenic emissions used for all run years? Are the MACC GFAS biomass burning emissions annually varying? What is done with soil NOx emissions? Is nudging off equivalent to a free running climate?

L245 Why compare OTD data from 1996-2000 with simulations of 2007-2011? Are these simulations with nudging on or off?

L353 Did you sample the model at TROPOMI overpass times, and then somehow produce the monthly mean values in Figure 9? Please clarify how you applied the averaging kernels to demonstrate that the model-satellite comparison is like-for-like.

L394 Clarify the plots in Figure 10 are all relative to CTH.

L422 Figure 11 I am unclear what the un-nudged runs represent. Do these runs somehow represent climate change over the 2001-2020 period, or are they completely unforced?