Parametrizing the mixing by clear air turbulence in the chemistry climate model EMAC and its respective radiative impact

Chau, Chun Hang; Hoor, Peter; Kaiser, Katharina; Tost, Holger

doi:10.5194/acp-26-3637-2026

Articles | Volume 26, issue 5

https://doi.org/10.5194/acp-26-3637-2026

© Author(s) 2026. This work is distributed under
the Creative Commons Attribution 4.0 License.

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The tropopause region in a changing atmosphere (TPChange)...

https://doi.org/10.5194/acp-26-3637-2026

© Author(s) 2026. This work is distributed under
the Creative Commons Attribution 4.0 License.

Articles | Volume 26, issue 5

Research article

|

11 Mar 2026

Research article |

| 11 Mar 2026

Parametrizing the mixing by clear air turbulence in the chemistry climate model EMAC and its respective radiative impact

Chun Hang Chau, Peter Hoor, Katharina Kaiser, and Holger Tost

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RC1:
'Comment on egusphere-2025-5382', Anonymous Referee #1, 01 Dec 2025

Dear Authors,
Please refer to attached PDF for comments.
Best,

Citation: https://doi.org/10.5194/egusphere-2025-5382-RC1
- AC1: 'Reply to RC1 and RC2 comments on egusphere-2025-5382', Chun Hang Chau, 15 Feb 2026
  
  Please find our reply attached as PDF.
  
  Citation: https://doi.org/10.5194/egusphere-2025-5382-AC1
RC2:
'Comment on egusphere-2025-5382', Anonymous Referee #2, 03 Dec 2025
Review of: “Parametrizing the mixing by clear air turbulence in the chemistry climate model EMAC and its respective radiative impact”

By: Chun Hang Chau, Peter Hoor, Katharina Kaiser, and Holger Tost

Recommendation: Reconsidered after major revisions

General comments:

The manuscript presents an attempt to include the effect of clear air turbulence (CAT) in the upper troposphere and lower stratosphere (UTLS) into a chemistry climate model (EMAC) via the implementation of a parametrisation submodel. Through the comparison between the model simulation with and without the parametrised effect of CAT, the effect of CAT on the distributions of ozone and other tracers is explored. The corresponding effect on radiative forcing is also examined.

However, in my opinion, there are some aspects of deficiency in the study, which require further development or explanation. These mainly concern the basic assumptions of the parametrisation scheme, the verification of the model results, and the interpretation of the major results. The details will be explained below. In view of that, I recommend major revisions before the manuscript is reconsidered.

Major comments:

1. First, I would like to clarify the major objective or aim of this study. In the abstract, or in lines 56-57, the major objective is deemed to be examining the sensitivity of UTLS chemistry and radiation on vertical turbulence mixing (as a side remark, I think it should be “the sensitivity of chemistry/radiation on CAT”, instead of the sentence structure used in the manuscript). However, there are only two model simulations with one having CAT included and the other serving as the control. If sensitivity is the focus of this study, should it be examined by varying the strength of the parametrised mixing by CAT? Please clarify if the term “sensitivity” means different from what is suggested here and explain how this is studied with just the MIX/NOMIX simulation-pair.

There is also another statement (lines 58-59), “We demonstrate the possibility of parametrizing CAT mixing based on turbulence indices”. However, if this is the major take-away from this manuscript, there should be a rigid evaluation or comparison to observations to validate that the strength of the mixing is reasonable or realistic. Since there is only one MIX experiment with one set of parameters selected, the authors need to elaborate on why this particular setting of the parametrisation scheme is chosen and is meaningful. Otherwise, the scientific relevance of the final conclusions, e.g. the –0.2 W/m² radiative forcing, is much diminished. Therefore, I urge the authors to clearly define the major goal of this study, or to put the study into a context, which shows that the current attempt is already a breakthrough (e.g. given the computational resources, such a parametrisation being included into a chemistry climate model is very difficult), in order to improve the scientific significance of the manuscript.

2. Second, I would like the authors to elaborate on their rationale for the CAT parametrisation scheme implemented. There are multiple assumptions behind this parametrisation scheme which require justification.

a) The flux of the tracer is assumed to be linearly proportional to the magnitude of the CAT index (equation 5). However, turbulence diagnostics like the Ellrod-Knox index, while having a certain degree of theoretical basis (e.g. the TI being linked to upper-level frontogenesis (Ellrod and Knapp, 1992), there is some empirical treatment (e.g. the constant C in the Ellrod-Knox index, equation 1 on page 5). Moreover, while stronger turbulence is assumed to be indicated by the higher magnitude of the turbulence diagnostics, the strength of turbulence is not assumed to be linearly proportional to the magnitude of the diagnostic (e.g. in Sharman et al. (2006), the mapping of indice to strength of turbulence is only piecewise linear; Sharman and Pearson (2017) use the log-normal distribution to map the diagnostic to eddy dissipation rate). Since there is no verification or comparison presented in the manuscript to show how realistic the mixing is in the MIX experiment, this assumption has to be justified.

b) The MoCATI is a new diagnostic, which is claimed to include the effect of stratification on turbulence. However, as noted in line 122, mixing is turned off above certain N_lim. Physically, the quantity that has such a role in turbulence would be the Richardson number, in which a value greater than the critical Richardson number would be stable (no turbulence). Nevertheless, Richardson number also takes into account the vertical wind shear, not only stratification. Therefore, this modification to the Ellrod-Knox has to be justified.

c) The important parameters, like C in equation 1, N_lim in equation 2, t_norm in equation 4, are only stated in the supplement without any description of how the authors came to this particular set of values. Are they tested for a range of values, and this set of values produces the most realistic tracer mixing? Or if the authors estimated reasonable values with some typical time or length scale/some other physical arguments? Or are they taken from other studies?

d) The decision to apply the mixing from 500 to 70 hPa (lines 107-108) may exclude some tropopause folds that intrude deep into the troposphere, which are hotspots of STE (e.g. Stohl et al., 2003) and CAT (e.g. Rodriguez Imazio et al., 2022). Will the effect of these events be excluded due to this choice?

Given that this parametrisation is the most important component of the study, it deserves a detailed and precise description.

3. Third, the authors should present better validation or evaluation of the performance of the new parametrisation scheme (that is based on MoCATI). For those presented in Sect. 3.1, they are mainly made between MoCATI and Ellrod-Knox index that are by definition (equation 2) highly correlated and dependent on each other. One can only see the effect of the additional “correction factor” based on stratification. The analysis done with TI being the reference is also confusing, as TI is yet another highly correlated turbulence diagnostic. Such analysis does not demonstrate the ability of MoCATI to realistically forecast CAT (TI is not a suitable “truth”) or show that the additional modification to Ellrod-Knox index is necessary. Therefore, I find Sect. 3.1 redundant, which at most only shows the internal consistency between MoCATI and Ellrod-Knox index (not surprising from the definition). In my opinion, the authors may directly argue that Ellrod-Knox index is a well-established CAT diagnostic (which only justifies its representation of the occurrence of CAT, not necessarily the strength of mixing), provided that the parametrisation produces realistic tracer mixing. However, concerning the performance of the parametrisation on the mixing of tracer, the only supportive evidence is Figure 7. The annual zonal mean ozone distributions of the simulations are compared to the satellite-based SWOOSH data, with the bias to observation in the MIX experiment being reduced. Nevertheless, the authors did not use it to help justify the validity of the parametrisation, but stated in lines 168-169 that such analysis (i.e. to see if CAT can improve representation of ozone in EMAC) is beyond the scope of the study. The authors should provide better arguments on the validity of the new parametrisation.

4. This comment concerns the major conclusions in Sect. 3.2.2 and 3.2.3. Since only one set of parameters for the CAT parametrisation is used to generate the MIX simulation, how confident are the authors in the changes to the tracer distribution or radiative effect? For instance, if the mixing is actually even stronger in reality (than that imposed by the parametrisation), would the distribution of tracer and the radiative effect be significantly different?

5. Also, water vapour is stated as playing an important role in radiation, but it is left out in the parametrisation due to technical issues. A major conclusion that is highlighted would be the –0.2 W/m² radiative effect at TOA. Will this number be changed (or even turn into a warming effect) if water vapour is included? If so, would the authors consider reminding readers of this limitation, like in line 14 “The global average radiative effect is about –0.2W/m²” and lines 253-254 “The simulation results show that the CAT mixing of tracers leads to a radiative cooling ... 208.9 mW/m².

6. Concerning the above major comments, I suggest the authors consider having a subsection to discuss the limitations of this study.

Specific comments:

Lines 37-38: For the citation of Kelvin-Helmholtz instability being related to vertical wind shear, I think it is more appropriate to also include other studies. E.g. the classics like Richardson (1920), or Dutton and Panofsky (1970).

Line 39: Dutton and Panofsky (1970) would be a suitable reference to link Kelvin-Helmholtz instability to the formation of CAT.

Lines 73-74: Could the authors comment on the vertical resolution near the tropopause? Since vertical wind shear is deemed important, the vertical resolution is of relevance to a reasonable representation of the vertical wind shear.

Lines 80-83: Could the authors provide some simple description of the different data sets? ( RC1-base-07, Ref-C1, CCMI, AMIP-II)? Like the statement of “historical hindcast” for CCMI-2022 Ref-D1.

Lines 115-117: The weighting constant C is likely to be resolution-dependent. In the supplement (Fig. S1), C has a magnitude of 0.1. How is this value set? Did the authors perform calibration for EMAC?

Lines 120-122: For the limitation threshold, did the authors perform analysis to support their choice of 6 × 10^-4 s^-1 (Fig. S1)?

Figure 1 and equation 3: In Figure 1, there are arrows in both directions. Is the flux from level n+1 to level n similarly parametrised? If so, it will give the net flux being (Χ_n – Χ_n+1) × CAT index (positive upward), which resembles the typical K-theory or flux-gradient theory for turbulent fluxes. Is this the case?

Equation 4, lines 129-130: Did the authors perform analysis to choose a particular value for t_norm? Which reference data is used to determine if it really “moderates the strength of mixing”?

Figure 2: Please check if the unit is correct. The Ellrod-Knox index in ERA5 reanalysis covers the order of magnitude from 10^-7 s^-2to barely reaching 10^-5 s^-2 (Lee et al., 2023) at 250 hPa. As the output of EMAC is coarser than ERA5, I expect a smaller value for Ellrod-Knox index (since the derivatives are most likely smoothened). However, the plot is showing values mainly in the 10^-6 to 10^-5 s^-2 values.

Lines 153-155: Could the authors clarify how the ROC analysis is performed? Am I correct that if TI exceeded a certain threshold (T1,2,3,4,5 in Figure 5), it is treated as the “ground truth” turbulence, then different values of the decision threshold of Ellrod-Knox index or MoCATI are used to verify against these TI-based “truth” to obtain the ROC curves? Apart from being unclear in this sentence, I am not convinced by using a highly related diagnostic (i.e. TI, on which Ellrod-Knox index is built) as the “truth” for CAT and verifying the performance of MoCATI or Ellrod-Knox index. Also, as mentioned in major comment 3, similar performance between MoCATI and Ellrod-Knox is expected, by definition. I therefore do not understand the inclusion of this analysis in the manuscript.

Lines 156-157: The effect of static stability is introduced into MoCATI, but whether it is realistic or not is not shown (being similar to Ellrod-Knox index does not support this statement).

Lines 160-169: What is the major message for this subsection? To me, it shows that the introduction of the parametrisation seemingly alleviates the bias and improves the representation of ozone in EMAC (when compared to observations). However, it is stated at the end that this is not in the scope of this study. It is a bit confusing, could the authors clarify?

Lines 184-186: The presence of mountains may trigger mountain wave turbulence, which is sometimes treated as part of CAT. Therefore, the presence of mountains may promote the excitation of gravity waves and locally stronger vertical wind shear. Could the authors elaborate on this statement of having fewer mountains resulting in stronger vertical wind gradients?

Line 207, equation R3: This equation seems to me not balanced, please check.

Lines 232-234: It is said that “O3 is relatively more sensitive to NOx (less sensitive to VOCs) than without the CAT mixing”. Is this concluded from the examination of FNR? FNR results are only mentioned later in the paragraph, so please consider rearranging the order.

Lines 230 and 235: Is there any reason why 800 hPa level also responds significantly?

Line 243: Could the authors explain if the values of 7.31 to 7.24 years of lifetime for CH4 are averaged vertically? I cannot match these values to the “global” line in Figure 11c and therefore ask.

Line 260: The reference to Figure 7a should probably be 7b or 7c?

Lines 276-289: When comparing the results to Riese et al. (2012), what is the role of water vapour? Since water vapour is not included in the CAT mixing parametrisation in EMAC, would that be even more important than the fact that the turbulent parametrisation schemes are different between CLaMS and EMAC?

Lines 314-317: Could the authors give a more detailed discussion on the possible effects of water vapour? Since it is mentioned to be of similar importance to ozone in terms of radiative effect, it would be great to inform the readers more about water vapour.

Lines 317-318: For different turbulence diagnostics, a calibration is necessary (concerning the mapping of their magnitude to the strength of turbulence, as mentioned in major comment 2a). Also, it may be interesting to explore the “sensitivity” of chemistry and radiation to the uncertainty of turbulence diagnostics (as each of them is designed to target different processes or derived empirically by different methods or data).

Technical corrections:

The entire manuscript:

Please improve the consistency of the terminology used in the manuscript. For instance, EMAC is referred to as “chemistry climate model” in the title, but also “climate chemistry model” subsequently (also whether or not to hyphenate).

Also, “Southern Hemisphere” is sometimes with upper and sometimes with lower case letters.

Please make sure the acronyms are introduced before they are used. For instance, MESSy is only introduced in line 69, but already used in line 58. Also, “UT” is only used once, without introducing it.

Line 300: typo of “ceO3”

References:

Dutton, J. A., & Panofsky, H. A. (1970). Clear air turbulence: A mystery may be unfolding. Science, 167(3920), 937–944. https://doi.org/10.1126/science.167.3920.937

Ellrod, G. P., & Knapp, D. I. (1992). An Objective Clear-Air Turbulence Forecasting Technique: Verification and Operational Use. Weather and Forecasting, 7(1), 150–165. https://doi.org/10.1175/1520-0434(1992)007<0150:AOCATF>2.0.CO;2

Ellrod, G. P., & Knox, J. A. (2010). Improvements to an Operational Clear-Air Turbulence Diagnostic Index by Addition of a Divergence Trend Term. Weather and Forecasting, 25(2), 789–798. https://doi.org/10.1175/2009WAF2222290.1

Lee, J. H., Kim, J. H., Sharman, R. D., Kim, J., & Son, S. W. (2023). Climatology of Clear-Air Turbulence in Upper Troposphere and Lower Stratosphere in the Northern Hemisphere Using ERA5 Reanalysis Data. Journal of Geophysical Research: Atmospheres, 128(1), e2022JD037679. https://doi.org/10.1029/2022JD037679

Richardson, L. F. (1920). The supply of energy from and to atmospheric eddies. Proceedings of the Royal Society of London. Series A, Containing Papers of a Mathematical and Physical Character, 97(686), 354–373. https://doi.org/10.1098/RSPA.1920.0039

Riese, M., F. Ploeger, A. Rap, B. Vogel, P. Konopka, M. Dameris, and P. Forster (2012), Impact of uncertainties in atmospheric mixing on simulated UTLS composition and related radiative effects, J. Geophys. Res., 117, D16305, doi:10.1029/2012JD017751.

Rodriguez Imazio, P., Dörnbrack, A., Urzua, R. D., Rivaben, N., & Godoy, A. (2022). Clear Air Turbulence Observed Across a Tropopause Fold Over the Drake Passage—A Case Study. Journal of Geophysical Research: Atmospheres, 127(4), e2021JD035908. https://doi.org/10.1029/2021JD035908

Sharman, R., Tebaldi, C., Wiener, G., & Wolff, J. (2006). An Integrated Approach to Mid- and Upper-Level Turbulence Forecasting. Weather and Forecasting, 21(3), 268–287. https://doi.org/10.1175/WAF924.1

Sharman, R. D., & Pearson, J. M. (2017). Prediction of Energy Dissipation Rates for Aviation Turbulence. Part I: Forecasting Nonconvective Turbulence. Journal of Applied Meteorology and Climatology, 56(2), 317–337. https://doi.org/10.1175/JAMC-D-16-0205.1

Stohl, A., Bonasoni, P., Cristofanelli, P., Collins, W., Feichter, J., Frank, A., Forster, C., Gerasopoulos, E., Gäggeler, H., James, P., Kentarchos, T., Kromp-Kolb, H., Krüger, B., Land, C., Meloen, J., Papayannis, A., Priller, A., Seibert, P., Sprenger, M., … Zerefos, C. (2003). Stratosphere-troposphere exchange: A review, and what we have learned from STACCATO. Journal of Geophysical Research Atmospheres, 108(12), 8516. https://doi.org/10.1029/2002JD002490
Citation: https://doi.org/10.5194/egusphere-2025-5382-RC2
- AC1: 'Reply to RC1 and RC2 comments on egusphere-2025-5382', Chun Hang Chau, 15 Feb 2026
  
  Please find our reply attached as PDF.
  
  Citation: https://doi.org/10.5194/egusphere-2025-5382-AC1
AC1: 'Reply to RC1 and RC2 comments on egusphere-2025-5382', Chun Hang Chau, 15 Feb 2026

Please find our reply attached as PDF.

Citation: https://doi.org/10.5194/egusphere-2025-5382-AC1

Peer review completion

AR – Author's response | RR – Referee report | ED – Editor decision | EF – Editorial file upload

AR by Chun Hang Chau on behalf of the Authors (15 Feb 2026) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (17 Feb 2026) by Huilin Chen

RR by Anonymous Referee #2 (19 Feb 2026)

Suggestions for revision or reasons for rejection

Recommendation: Accepted subject to minor revisions

I would like to thank the authors for their effort to improve the manuscript and take into account the comments given. I find the research objective of the study and the description of the CAT submodel are much more clearly stated in this revised version of the manuscript. Also, the additional comparison to the new simulation (QCTM-MIX-ENI) and restructuring of the parts related to SWOOSH data addresses my major concern for the original manuscript. I only have minor comments on the discussion of the results or the outlook of the revised manuscript. Therefore, I suggest accepting the manuscript subject to minor revision.

Comments:

1. The extra simulation QCTM-MIX-ENI (Fig. 2, Table 3):
Thanks a lot for including this additional simulation (QCTM-MIX-ENI) and I find it useful to demonstrate the need for the modification based on stratification to the Ellrod-Knox index to generate realistic turbulent mixing of tracers. I can now better understand the rationale for introducing the stability term for MoCATI. Much appreciated for this extra work.

As a side remark, I think Fig. 2 also shows that probably the Ellrod-Knox index (and hence likely carried over to MoCATI) has its own limitation. First, it is based on dry dynamics, which most likely misses turbulence mixing with are more related to convective sources (e.g. near-cloud turbulence), especially in the tropics. Also, the Ellrod-Knox index was normally validated with pilot reports at a lower altitude (~200 to 300 hPa), which may not be optimal for diagnosing CAT at higher altitudes that in general have enhanced stratification. It is therefore a good idea to test other turbulence diagnostics with different characteristics, as stated in Sect. 4.

2. Result discussion on the radiative impact (Sect. 3.3)
Thanks for informing the readers more about the role of water vapour in the revised manuscript. It is mentioned in the reply document that preliminary results of a simulation that includes the effect of water vapour considered (by nudged dynamics) still show an overall cooling. I think this fact may strengthen the argument that the difference in the radiative impact (to Riese et al. 2012) is due to the different parametrisation schemes in CLaMS and EMAC, but not because of the fact that the (expected) warming effect of water vapour is not included in the current study. However, this is only a suggestion, and the authors should consider whether this is an overstatement.

3. Outlook on future work (Sect. 4)
I also encourage the authors to extend the outlook section a bit further. Given that the cooling effect found in this study is different from the warming effect concluded from the previous study, would the authors suggest possible ways to verify the simulation results? Related to Comment 1, maybe “the pros and cons” (line 334) can be a bit more specific.

Technical corrections:
Tropopause definition for Fig. 2 and other figures: After the restructuring of the original Sect. 3.1, seemingly there is no description of the definition of tropopause. I assume it should still be the lapse rate tropopause? Consider inserting this information at a suitable place.

Unit of t_norm in Table 2: Compared to the reply document, it is stated that t_norm is dimensionless. I am a bit confused by the unit here.

Typo of “QCTM-MIX-ERI": e.g. line 177 and in Table 3.

Line 156: I think it is the mapping function being piece-wise linear - “while the mapping functions between the strength ...”

Line 163: “In order to ... CAT submodel, a comparison ...”

Line 185: “potential impact of tracers by the mixing algorithm of CAT”

Line 317: “while in the extra-tropics"

Line 333: “The CAT submodel also has the option ...”

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ED: Publish subject to minor revisions (review by editor) (20 Feb 2026) by Huilin Chen

AR by Chun Hang Chau on behalf of the Authors (28 Feb 2026) Author's response Author's tracked changes Manuscript

ED: Publish as is (04 Mar 2026) by Huilin Chen

AR by Chun Hang Chau on behalf of the Authors (05 Mar 2026) Manuscript

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Short summary

This study examines the potential impact of different greenhouse gases to vertical mixing by clear air turbulence in the upper troposphere and lower stratosphere . We found that ozone is most sensitive to vertical mixing and could lead to cooling at the top of the atmosphere by -0.2 W/m2. We also found that the vertical mixing by clear air turbulence could lead to changes in atmospheric chemistry including changing the methane lifetime and the ozone sensitivity.