Improvement and further development in CESM/CAM5: gas-phase chemistry and inorganic aerosol treatments

He, J.; Zhang, Y.

doi:https://doi.org/10.5194/acp-14-9171-2014

Articles | Volume 14, issue 17

https://doi.org/10.5194/acp-14-9171-2014

© Author(s) 2014. This work is distributed under
the Creative Commons Attribution 3.0 License.

https://doi.org/10.5194/acp-14-9171-2014

© Author(s) 2014. This work is distributed under
the Creative Commons Attribution 3.0 License.

Articles | Volume 14, issue 17

Research article

|

08 Sep 2014

Research article |

| 08 Sep 2014

Improvement and further development in CESM/CAM5: gas-phase chemistry and inorganic aerosol treatments

J. He and Y. Zhang

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Final revised paper (published on 08 Sep 2014)
Supplement to the final revised paper
Preprint (discussion started on 28 Oct 2013)

Interactive discussion

Status: closed

AC: Author comment | RC: Referee comment | SC: Short comment | EC: Editor comment

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- Supplement

RC C10245: 'Reviewer's comments', Anonymous Referee #1, 19 Dec 2013
- AC C13029: 'Reply to Referee 1', Yang Zhang, 27 Mar 2014
RC C10379: 'Review', Anonymous Referee #2, 23 Dec 2013
- AC C13041: 'Reply to Referee 2', Yang Zhang, 27 Mar 2014
RC C10396: 'Reviewer Comments', Anonymous Referee #3, 24 Dec 2013
- AC C13051: 'Reply to Referee 3', Yang Zhang, 27 Mar 2014
SC C10406: 'Review of the manuscript entitled “Improvement and further development in CESM/CAM5: gas-phase chemistry and inorganic aerosol treatments” by He and Zhang submitted for possible publication in the ACP', Shaocai Yu, 24 Dec 2013
- AC C13046: 'Reply to Referee 4', Yang Zhang, 27 Mar 2014

Peer-review completion

AR: Author's response | RR: Referee report | ED: Editor decision

AR by Yang Zhang on behalf of the Authors (27 Mar 2014) Author's response

ED: Referee Nomination & Report Request started (13 Apr 2014) by Xiaohong Liu

RR by Anonymous Referee #1 (24 Apr 2014)

Suggestions for revision or reasons for rejection

The authors have made a substantial effort to revise the manuscript. Specifically, they have conducted three additional 5-year integrations using prescribed SST. The results of these runs provide a much more solid base comparing to those previous 1-year runs for the performance evaluation of the new model, especially in simulating atmospheric chemistry and aerosol life cycle. I also admire the authors’ effort to reemphasize their discussions on science rather than model development related topics, and also to accommodate many suggestions from the reviewers. The revised manuscript appears to be a significant improvement from the original one. In their responses and also revisions, the authors have addressed many of my concerns raised in previous review. There are, however, still a few remaining issues for the authors to improve in my opinion. The following comments are provided for the authors to consider when making their revision.

The first issue I see a room for improvement is regarding the discussions on modeled changes of meteorological/climate variables. Specifically speaking, these include the changes of T2, Q2, WS10, precip, and PBLH. Discussions on radiative variables and cloud forcing are fine. The reason is rather simple and actually explained in my previous comment regarding the 1-year transient configuration, that is the changes of these meteorological/climate variables mostly represent exaggerated transient responses (mostly noise in other words) due to the model configuration (mainly ocean response). The adoption of climatological SST or the so-called AMIP (Atmospheric Model Intercomparison Project) configuration is an excellent choice because ocean controls to a great extent the climate responses, and observed SST largely reflects actual responses of the climate system to anthropogenic forcings. This is why such a configuration is commonly used when modeled physical or chemical features rather than dynamical feedbacks to these features are concerned. To interpret the changes of climate/meteorological variables in this configuration, however, should be constrained or simply avoided particularly when dealing with water cycle because of the stiff atmosphere-ocean interface due to prescribed SST. Again, the purpose of this paper is to demonstrate the difference in modeling chemistry and aerosol features of the new model components brought to CESM, for discussion on climate consequences, more sophisticated configuration and much longer integration time would be needed. Papers that do not follow the correct procedure might make to the “news” but would not stand long.

Several specific comments.

1. Line 23, suggest adding “thus could” before “improve model performance”; the same applies to Line 27, suggest using “could further improve” instead of “further improves”.

2. Line 32, suggest deleting “as well as near-surface … precipitation”.

3. Line 76, “…of these aerosols”, perhaps should say “of these aerosol constituents” instead.

4. Line 101-135, a very brief (1~2 sentences) summary of the major features and differences of these various schemes might be very useful.

5. Line 198-217 and other places: please make it clear enough to a wide reader group that this “J value” is referring to “nucleation rate”, not “photolysis rate”. The latter is commonly used in atmospheric chemistry literature.

6. Line 237-239, “given their…” this sentence could be revised, e.g., “giving the high computational cost due to …”.

7. Line 325-326, “All production… December 31, 2005” duplicates the previous sentence.

8. Line 387, “discussed below. That” to “discussed below, that”.

9. 4. Model Evaluation: again, here and in many other places, I’d suggest the authors to remove “meteorological” and discussions of changes of T2, Q2, and WS10 from the text and Tables. The authors could make a clear statement that the major interest of this paper is to evaluate the model performance in atmospheric chemistry and aerosol simulations.

10. Line 445: the authors might want to use a commonly used unit for OH in molecules/cm^3.

11. General comment on “5. Impacts …2001 Predictions”, perhaps more adequate terms than “2001 predictions” are “sensitivity simulations”. If prescribed 5-year SST run is computational demanding, the discussion in this section should emphasize more on the nature of these sensitivity tests exploring the differences brought by various schemes. Also, wondering if the authors want to add a few comments to compare 5.5 and later 6 (i.e., 5-year integration), because the latter demonstrates a better evaluation base for the model performance.

12. Line 945, “increases over global with a…”, indicate increases from what. There are many other similar sentences.

13. Line 950-955, again these should be avoided.

14. Line 971, “most gas species”, did the authors mean “gaseous aerosol precursors”? Line 972, “more accurate aerosol thermodynamic treatments”, is this referring to the extremely low accommodation coefficients (actually discussed a few lines later)?

15. Line 976, “previous works”, the authors might want to provide references for this, either here or in later discussion.

16. Line 979-981, “SO4= burden higher…due to greater SO2 oxidation” seems inconsistent with higher H2SO4 “due to lower mass accommodation coefficient”. Is “oxidation” here referring to aqueous phase oxidation? If so, please make it clear.

17. Line 983-984, it seems that dry deposition change is less likely to cause such a change in carbonaceous aerosol burden, also “slower … aging rate” seems inconsistent with higher H2SO4.

18, Line 1025-1040, it’s better to delete “T2”, “Q2”, “WS10”, “precip”, “meteorological” from the discussion, here and elsewhere.

19. Tables. It is odd not listing the mean values of modeled variables while listing their observed values in Table 3 – Table 7. Table 1, purpose column of MAM_NEW_5YB, “Earth’s components” reads odd.

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RR by Anonymous Referee #3 (29 Apr 2014)

Suggestions for revision or reasons for rejection

The original manuscript did not provide adequate details on how the authors have implemented ISORROPIA II (a bulk thermodynamic equilibrium model) in CAM5 to perform size (mode) resolved gas-particle partitioning of sulfate, nitrate, chloride, and ammonium. The authors now state that they actually use a kinetic approach, but unfortunately offer no details on how exactly this is done. Below are some questions that need to be answered to better understand their approach:

1) How exactly do the authors calculate the driving forces for mass transfer for each species to each mode?

2) What do the authors mean by “Since by default the model treats the condensation of inorganic volatile gas species as irreversible process (no evaporation), …”? What is this so-called “default,” and why does it treat condensation of volatile species as if they are non-volatile? This basic foundation of their kinetic approach appears to be questionable, but I cannot comment on it further until I have more details on it.

3) How does the kinetic approach ensure electroneutrality in each mode after kinetically condensing H2SO4, NH3, HNO3, and HCl at different rates (using different accommodation coefficients)?

4) The authors say that evaporation is not treated in the model, so then how would HCl evaporate from sea salt when H2SO4 and HNO3 condense on it?

5) The authors need to provide mathematical proof for their claim that the lower limit of mass accommodation coefficients correspond to uptake coefficients, which represent the net fluxes.

6) Again, ignoring coarse mode sea salt and dust from participating in gas-particle partitioning of H2SO4, HNO3, and HCl is a gross oversimplification. Since the authors are using some sort of a kinetic approach, why cannot the coarse modes be also included in the gas-particle partitioning calculation?

7) Why was NH3(g)/NH4+ not added to cloud water?

Again, these issues must be clearly addressed before the present work can be considered an improvement to the existing CAM5.1 model. I cannot recommend that the manuscript be accepted or rejected until the authors clearly explain their approach with enough detail such that the reader can reproduce the kinetic approach (using ISORROPIA II) on their own. The authors are requested to not simply cite some other reference(s) for details on the present approach to circumvent the issues outlined above.

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ED: Reconsider after major revisions (01 May 2014) by Xiaohong Liu

AR by Yang Zhang on behalf of the Authors (14 May 2014) Author's response Manuscript

ED: Referee Nomination & Report Request started (23 May 2014) by Xiaohong Liu

RR by Anonymous Referee #3 (05 Jun 2014)

Suggestions for revision or reasons for rejection

General Comments:
I have carefully read the authors’ responses to my questions. While some details still remain unclear, I have understood the basic formulation of their kinetic mass transfer treatment (using ISORROPIA for thermodynamics) for HNO3 and HCl. I find this treatment to be completely ad hoc and scientifically flawed as detailed below. Also, by the authors’ own admission, the treatment is incomplete as it currently ignores coarse mode sea salt and dust particles from participating in gas-particle partitioning of HNO3 and HCl. Finally, the performance of this treatment against a benchmark kinetic treatment is neither shown in this paper nor previously documented. While the authors argue that their treatment can be further improved in the future when additional resources (both human and computer) are available, I contend that the basic foundation of their treatment is flawed and that it cannot be improved by additional resources – they would need a completely new foundation to extend the kinetic treatment to coarse mode particles.

It is my opinion that model improvement and development papers should carry the extra burden of very clearly describing and validating the proposed new treatment(s) so that potential users of the new/improved model are aware of its strengths and limitations and do not misinterpret the results. Evaluation using field observations is of course important (as done in this paper), but it cannot be considered as validation when we know that the new treatment is incomplete and involves several assumptions whose validity have not been independently verified. The present manuscript fails to meet this basic criterion for a model improvement/development paper. Unfortunately, therefore, I must strongly recommend that this manuscript be rejected.

Detailed Comments
1) In response to my question on how the driving force for mass transfer for each species to each mode is calculated, the authors gave the description of mass transfer coefficient. Calculation of mass transfer coefficient is quite trivial and that is not what I had asked for. It is common knowledge that driving force is defined as the difference between the bulk gas-phase concentration of a species and the gas-phase concentration at the surface of the particles that is in equilibrium with particle-phase concentration. It is not at all clear how the authors calculate the driving forces for the mass transfer of HNO3 and HCl to each mode. If they perform bulk equilibrium calculation with ISORROPIA to get the driving forces then it is an incorrect approach. While it may yield a reasonably ok solution (although I am not sure it does in the present case) for gas-phase concentrations, it does not capture the correct distribution of nitrate and chloride amongst the different aerosol modes. This is because the driving forces for each species over each mode can be very different (depending on their composition), which are not possible to obtain with a bulk equilibrium calculation. This is the crux of the problem.

2) The authors say that they have adopted the default mass transfer treatment in CAM5.1 to do kinetic mass transfer of HNO3 and HCl. This is a serious flaw, because the default treatment of irreversible condensation is really only valid for non-volatile species such as H2SO4. It may be ok to extend it to NH3 in the absence of HNO3 and HCl, but it is certainly not appropriate in a general situation when all four species may be present at the same time. Thus the basic foundation of their kinetic treatment is flawed.

3) The authors argue that the use of the lower limit values of accommodation coefficient in an irreversible condensation approach compensates for the loss due to evaporation process. This reasoning is also flawed. Tuning accommodation coefficient will speed up or slow down condensation rate, but the final value in each mode depends on its thermodynamic driving force which is not properly accounted for in the present treatment. The authors themselves allude to this problem in the text to explain the significant overprediction of nitrate and chloride for CONUS and Europe.

4) Finally, I reiterate that ignoring coarse mode sea salt and dust from participating in gas-particle partitioning of H2SO4, HNO3, and HCl is a gross oversimplification. The coarse mode will have significant impact on the distribution of nitrate and chloride amongst different modes. The current treatment is therefore incomplete and cannot yield reliable results. As the current kinetic treatment for fine modes is flawed, it would be a mistake to try to somehow extend it to coarse mode with additional computation and human resources.

5) In conclusion, I would like to emphasize that solution to kinetic partitioning of HNO3 and HCl to particles of all sizes and any composition is not trivial. The treatment proposed by authors is completely ad hoc and seriously flawed. It is also not clearly described in the paper (after several rounds of review) and its performance against a benchmark treatment under well-defined initial conditions (in a box model setting) has not been documented. It is therefore premature to implement it straightaway in a global model and evaluate it with field observations. Just because it is computationally efficient does not automatically mean it can be reliably used to perform long-term climate simulations.

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ED: Publish subject to technical corrections (15 Jul 2014) by Xiaohong Liu

AR by Yang Zhang on behalf of the Authors (24 Jul 2014) Manuscript

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