the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 11 Dec 2023
An analysis coordinate transform to facilitate use of in-situ aircraft observations for flux estimation
Abstract. Analysis of aircraft observations of atmospheric trace gases is key towards improving our understanding of fundamental chemical processes and quantifying anthropogenic emissions. A common approach for such analysis is use of chemical transport models to produce 4-D fields for comparison with these observations together with various inversion techniques to constrain the underlying fluxes and chemistry. Yet, time and monetary constraints of expensive computational jobs for chemical transport modelling can be a significant hindrance. Here, we show the advantages of using potential temperature as a dynamical coordinate to compare such simulations to aircraft observations of trace gases whose concentration fields are strongly influenced by synoptic-scale transport. We use global observations of ethane and propane from the Atmospheric Tomography (ATom) aircraft mission and simulate global mole fractions for these gases using GEOS-Chem High Performance v13.4.1. We show, using potential temperature as an analysis coordinate, that Bayesian estimates of the fluxes of these gases in the Northern Hemisphere are largely invariant (± 10 %) even as the simulation spatial resolution is increased 100-fold. Our approach can have broad applications for the modelling of trace gases in the extra-tropics, particularly those with lifetimes long compared to synoptic timescales.
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RC1: 'Comment on egusphere-2023-2227', Anonymous Referee #1, 15 Jan 2024
This paper presents a case study of using a previously developed Bayesian approach to evaluate emission estimates of C3H8 and C2H6 from global model simulations and aircraft observations from the ATom campaign. The paper compares 3 different model simulations and demonstrates that the results are less dependent on model resolution when using potential temperature (Tpot) rather than pressure as coordinate. The main conclusion of this study is that using Tpot can safe efforts and costs since coarse resolution simulations are sufficient and provide similar results as more costly high resolution runs.
The case study per se could be of interest, specifically to other studies using ATom data, modelers or developers of emission inventories, but in my view there is significantly more work needed before the paper is ready for publication and can provide value to the scientific community. Below some of my major concerns:
*) Throughout the paper the paper lists a number of limitations on when the methodology can be used and they also applied significant filtering to the data set. More information is needed on how the authors decided on the different filtering and how this could be generalized and be applicable to other cases. How could you decide if this method is applicable and valid when multiple resolution simulations are not done? Have you tested in with other species of lifetimes ~10 days or longer (e.g. CO?)
*)The highest resolution tested is 0.5x0.625 deg which is still fairly coarse. I suggest to make very clear that this methodology has only been tested on model resolutions global climate models are generally run at.
*) Could you please confirm that all simulations use the same base emissions and also state what inventory they are based on. It was not clear from the description. Also in Line 91 it is not clear what is scaled how? You substituted C3H8 with default C2H6? Are there no C3H8 emissions available?
*) It is highly concerning that the simulations experiences negative concentrations and that this has been fixed by simply setting these to zero. Negative concentrations indicate an issue in the model or the setup and this simple non-physical fix does not provide high confidence in the model results. If this is a general issue and solution with the model and well documented that this does not lead to issues in the simulated fields, then this needs to be referred to in the paper.
*) I do not see convincing information that the emission estimates are less resolution dependent using Tpot compared to pressure. E.g., how would Figure 4 look were you to use pressure. Or how would the numbers in Table 1 change if the emission estimates are using pressure as coordinate?
*) Figure 2 and 3: the 0.5x 0.625 degree runs look significantly different from the coarser resolution results for 23 Feb for both pressure and Tpot. How do the authors explain this?
*) Need to specify r2, rmse etc. for Figure 4 and related Figures in Supplement.
*) The results section needs to be separated into a methodology and an actual results/discussion section.
Methodology: Please be clear how you averaged and filtered the data. To what degree does the +/- 5 days sampling before and after the observation time contribute to reducing the resolution dependence? Effectively you degrade the higher model resolutions more than the coarsest.*) Significantly more in-depth analysis and discussion on the results are needed (see comments above). The confidence range in Table 1 does not provide a strong indication for missing sources. Without knowing what the base emissions are, whether they are representative for the year and how they compare to other inventories, you cannot say that there are missing sources but differences could also be due to uncertainties in emission factors, underestimation of emissions from specific sectors etc. It is also not clear to me, if the emissions were scaled upfront by 1.1 and 1.2 for C2H6 and C3H8, respectively and the scaling factors (Table 1) are in the order 0.8-1(1.1) and 0.9-1.1(1.2), then the original emissions might not be too low at all if the lower ranges apply.
Table 1 results for the highest resolution run are actually more different from the two other simulations. This might be related to my question related to Figures 2&3 or simply indicates that there is still some resolution dependence? Have you rerun your simulations with the lower and upper ranges of your estimates to see whether you improve the comparison to aircraft data?
It also needs to be clearly stated how much new information this study provides beyond what has been done in Tribby et al. (2022).*)The paper is missing a Summary/Conclusion.
Citation: https://doi.org/10.5194/egusphere-2023-2227-RC1 -
AC1: 'Reply on RC1', Ariana Tribby, 13 Aug 2024
The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2023/egusphere-2023-2227/egusphere-2023-2227-AC1-supplement.pdf
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AC1: 'Reply on RC1', Ariana Tribby, 13 Aug 2024
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RC2: 'Comment on egusphere-2023-2227', Anonymous Referee #2, 29 Jan 2024
This paper presents a Bayesian inversion estimating ethane and propane emissions using aircraft data from the ATom campaigns and GEOS-Chem predictions at different horizontal resolutions (4x5, 2x2.5, and 0.5x0.625 degrees nested). The authors argue that the use of potential temperature as a zonal coordinate results in a comparison to aircraft data that is less sensitive to model resolution than comparisons on lat-lon-pressure coordinates, and inversions for longer-lived trace gas species can thus be performed at coarser resolution to save time and cost.
While the results of this study certainly have potential value for other work quantifying sources of longer-lived trace gases, this paper is not suitable for publication without major revisions. As is, it assumes the reader is intimately familiar with the previous study on which it is based (Tribby et al., 2022), and reads as a sort of proof-of-concept of that specific work (a Bayesian inversion based on 4x5 degree model predictions and comparisons to ATom data on potential temperature coordinates). More detail is needed throughout the paper in order for this to serve as a standalone study. A discussion and conclusions section are also needed after the Results section to demonstrate the broader context of this work and its applicability to other research problems (and to complete the paper!). Also, many of the claims made throughout the paper are currently too qualitative, and the authors must do more to quantify their findings and demonstrate how they improve upon inversions using lat-lon-pressure coordinates. I also question whether the analysis used is the best approach for testing their hypothesis. I have made specific line-by-line suggestions below.
Specific comments:
Lines 46-51: More information about the data exclusion process here is needed. Presumably these are being done to limit the dataset to those observations whose variance is dominated by synoptic-scale transport from the midlatitudes? How do the authors confirm their screening can “sufficiently reduce subtropical influence”? How do the results vary if these screening criteria are changed, and what recommendations can the authors make for other studies using this approach?
Lines 90-93: Please note which emission inventories were used rather than just referring to them as “default”. Also, please explain how the scaling factors for the ethane and propane emissions were derived. I think I found the details in Tribby et al. (2022)—they are related to observed ethane:propane ratios?-- but more information is needed here.
Line 99: While I see how some of variability across latitude is maybe collapsed when moving from pressure to potential temperature coordinates, the differences between Figure 2 and 3 are pretty subtle and I disagree with the authors’ claim that the curtain plots in Figure 3 look “very similar” at the different horizontal resolutions. A more quantitative comparison of the differences between simulations is warranted here.
Line 122-127 and Figure 4: A visual inspection is not sufficient here. Please provide some quantitative statistics to demonstrate good agreement between the simulations and aircraft data at all three horizontal resolutions and with the inclusions of the +/- 5 day window when using potential temperature as a coordinate. Also, please show how these statistics are improved relative to a comparison using lat-lon-pressure coordinates. Lastly, why was the 5-day time window chosen for comparison?
Line 137-150: This should all be moved to the Methods section rather than the Results.
Lines 151-158 and Table 1: This section needs the most additional work to be useful to the broader community. At the very least, it must include a comparison to inversions using lat-lon-pressure coordinates to prove that the resulting alpha is less dependent on model resolution when using potential temperature. Also, while the authors mention they did one test using the 4x5 degree simulated data as the observations in a 0.5x0.625 degree inversion, I question why the authors rely mostly on inversions using real observations rather than simulated ones in this analysis. It seems much easier to quantify the reliability of the results in the latter case, when the true flux is known and can be perturbed. Also, on that note, the authors need to address why the 95% credible interval is [0.71, 0.86] in the simulated inversion—shouldn’t it be approaching 1.0 in this case? I’m unclear if that’s the case for the inversion using real observations, but more discussion is needed to explain the behaviors here. Also, how dependent are the results on the spatial distribution of the emissions (i.e. if the authors used a prior with the same global flux but different spatial distribution)? Such a test would help demonstrate the limitations and applicability of this work in other contexts.
Technical comment:
Line 102: I think this should be referring to Figures S4-S7?
Citation: https://doi.org/10.5194/egusphere-2023-2227-RC2 -
AC2: 'Reply on RC2', Ariana Tribby, 13 Aug 2024
The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2023/egusphere-2023-2227/egusphere-2023-2227-AC2-supplement.pdf
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AC2: 'Reply on RC2', Ariana Tribby, 13 Aug 2024
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RC3: 'Referee comment on Tribby and Wennberg', Anonymous Referee #3, 31 Jan 2024
Tribby and Wennberg argue in “An analysis coordinate transform to facilite use of in-situ aircraft observations for flux estimation” that simulated ethane and propane fields from the GEOS-Chem transport model run at three different horizontal resolutions look similar when the chemical tracer is plotted on a latitude versus potential temperature coordinate, although they look different when plotted on a latitude versus pressure coordinate. They then conduct a simple optimization in which the simulated mole fractions are compared to observed mole fractions from the ATom campaign, at the same latitude and potential temperature, and scaled to match. Tribby and Wennberg report that the scale factor is within 10% for simulations whose resolution ranges from 4x5 deg to 0.5x0.625 deg. They use this agreement to conclude that the use potential temperature as the analysis coordinate for comparing simulated to observed tracers could save time and money associated with chemical transport modeling.
The analysis in the paper was insufficient to substantiate this conclusion, and major revisions and additional writing are required before the paper is suitable for publication.
There was no counterfactual presented, in terms of how close the optimization scale factors would be if a comparison were conducted in latitude/altitude space rather than latitude/potential temperature space. This comparison is critical to evaluate the authors’ conclusion about the benefits of the proposed coordinate transform.
There was no argument offered for the appropriate spatial resolution at which fluxes could be optimized. While the methods were not clear, I got the impression that the authors were optimizing fluxes uniformly or perhaps zonally, both of which would be coarser than what is desired for many chemical species. The authors do not show whether (or how) this approach could be used to improve flux optimizations at continental, regional, or local scales, where fluxes would be optimized on a 2-d grid rather than a zonal a.
The spatial scales of the chemical transport model were also coarse compared to that which would be desired for some applications (e.g., 10s of km), and it is not clear whether this approach would add value at those scales.
The authors simulate the chemical fields using fluxes that had previously been optimized in Tribby et al., 2022. Can this approach work when there are spatial biases in the distribution of prior fluxes fluxes (for example, zonal, meridional, or seasonal biases) imposed in the chemical transport model? If so, what are the limitations that are important for users of this approach to take into account?
The authors describe the results plotted in Fig. 3 as being more consistent across resolutions than those plotted in Fig. 2, although the results for February 23 look quite different among the three resolutions even in Fig. 3. On this day, there are elevated concentrations in isolated patches within the middle of the free troposphere apparent in the 0.5x0.625 deg simulation, but not in the other simulations. The ATom observations are not shown for this day, so it is not clear whether the elevated concentrations were observed or whether they are an artifact of the the transport model. In either case, the paper should discuss what characteristics of the meteorology on this day lead to the result that the potential temperature approach does not lead to convergence among the various resolutions.
In general, the paper read as incomplete. It is noteworthy that the paper did not have a Discussion or Conclusions section. This should be remedied before a revision is considered. It ends abruptly and leaves the reader with many questions, and it is surprising that the paper went out for review. The methods section lacked sufficient detail to understand the simulations and emissions inventories underlying the simulations. I am not familiar with Tribby et al., (2022), and relevant aspects of the methodology, results, and conclusions should be summarized briefly so that readers of this paper are not required to do an in-depth read of that paper. The results section did not contain the relevant analysis and documentation to substantiate the conclusioins (as described above), and the lack of discussion meant that it is not clear what the caveats of employing this method were.
Citation: https://doi.org/10.5194/egusphere-2023-2227-RC3 -
AC3: 'Reply on RC3', Ariana Tribby, 13 Aug 2024
The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2023/egusphere-2023-2227/egusphere-2023-2227-AC3-supplement.pdf
-
AC3: 'Reply on RC3', Ariana Tribby, 13 Aug 2024
Interactive discussion
Status: closed
-
RC1: 'Comment on egusphere-2023-2227', Anonymous Referee #1, 15 Jan 2024
This paper presents a case study of using a previously developed Bayesian approach to evaluate emission estimates of C3H8 and C2H6 from global model simulations and aircraft observations from the ATom campaign. The paper compares 3 different model simulations and demonstrates that the results are less dependent on model resolution when using potential temperature (Tpot) rather than pressure as coordinate. The main conclusion of this study is that using Tpot can safe efforts and costs since coarse resolution simulations are sufficient and provide similar results as more costly high resolution runs.
The case study per se could be of interest, specifically to other studies using ATom data, modelers or developers of emission inventories, but in my view there is significantly more work needed before the paper is ready for publication and can provide value to the scientific community. Below some of my major concerns:
*) Throughout the paper the paper lists a number of limitations on when the methodology can be used and they also applied significant filtering to the data set. More information is needed on how the authors decided on the different filtering and how this could be generalized and be applicable to other cases. How could you decide if this method is applicable and valid when multiple resolution simulations are not done? Have you tested in with other species of lifetimes ~10 days or longer (e.g. CO?)
*)The highest resolution tested is 0.5x0.625 deg which is still fairly coarse. I suggest to make very clear that this methodology has only been tested on model resolutions global climate models are generally run at.
*) Could you please confirm that all simulations use the same base emissions and also state what inventory they are based on. It was not clear from the description. Also in Line 91 it is not clear what is scaled how? You substituted C3H8 with default C2H6? Are there no C3H8 emissions available?
*) It is highly concerning that the simulations experiences negative concentrations and that this has been fixed by simply setting these to zero. Negative concentrations indicate an issue in the model or the setup and this simple non-physical fix does not provide high confidence in the model results. If this is a general issue and solution with the model and well documented that this does not lead to issues in the simulated fields, then this needs to be referred to in the paper.
*) I do not see convincing information that the emission estimates are less resolution dependent using Tpot compared to pressure. E.g., how would Figure 4 look were you to use pressure. Or how would the numbers in Table 1 change if the emission estimates are using pressure as coordinate?
*) Figure 2 and 3: the 0.5x 0.625 degree runs look significantly different from the coarser resolution results for 23 Feb for both pressure and Tpot. How do the authors explain this?
*) Need to specify r2, rmse etc. for Figure 4 and related Figures in Supplement.
*) The results section needs to be separated into a methodology and an actual results/discussion section.
Methodology: Please be clear how you averaged and filtered the data. To what degree does the +/- 5 days sampling before and after the observation time contribute to reducing the resolution dependence? Effectively you degrade the higher model resolutions more than the coarsest.*) Significantly more in-depth analysis and discussion on the results are needed (see comments above). The confidence range in Table 1 does not provide a strong indication for missing sources. Without knowing what the base emissions are, whether they are representative for the year and how they compare to other inventories, you cannot say that there are missing sources but differences could also be due to uncertainties in emission factors, underestimation of emissions from specific sectors etc. It is also not clear to me, if the emissions were scaled upfront by 1.1 and 1.2 for C2H6 and C3H8, respectively and the scaling factors (Table 1) are in the order 0.8-1(1.1) and 0.9-1.1(1.2), then the original emissions might not be too low at all if the lower ranges apply.
Table 1 results for the highest resolution run are actually more different from the two other simulations. This might be related to my question related to Figures 2&3 or simply indicates that there is still some resolution dependence? Have you rerun your simulations with the lower and upper ranges of your estimates to see whether you improve the comparison to aircraft data?
It also needs to be clearly stated how much new information this study provides beyond what has been done in Tribby et al. (2022).*)The paper is missing a Summary/Conclusion.
Citation: https://doi.org/10.5194/egusphere-2023-2227-RC1 -
AC1: 'Reply on RC1', Ariana Tribby, 13 Aug 2024
The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2023/egusphere-2023-2227/egusphere-2023-2227-AC1-supplement.pdf
-
AC1: 'Reply on RC1', Ariana Tribby, 13 Aug 2024
-
RC2: 'Comment on egusphere-2023-2227', Anonymous Referee #2, 29 Jan 2024
This paper presents a Bayesian inversion estimating ethane and propane emissions using aircraft data from the ATom campaigns and GEOS-Chem predictions at different horizontal resolutions (4x5, 2x2.5, and 0.5x0.625 degrees nested). The authors argue that the use of potential temperature as a zonal coordinate results in a comparison to aircraft data that is less sensitive to model resolution than comparisons on lat-lon-pressure coordinates, and inversions for longer-lived trace gas species can thus be performed at coarser resolution to save time and cost.
While the results of this study certainly have potential value for other work quantifying sources of longer-lived trace gases, this paper is not suitable for publication without major revisions. As is, it assumes the reader is intimately familiar with the previous study on which it is based (Tribby et al., 2022), and reads as a sort of proof-of-concept of that specific work (a Bayesian inversion based on 4x5 degree model predictions and comparisons to ATom data on potential temperature coordinates). More detail is needed throughout the paper in order for this to serve as a standalone study. A discussion and conclusions section are also needed after the Results section to demonstrate the broader context of this work and its applicability to other research problems (and to complete the paper!). Also, many of the claims made throughout the paper are currently too qualitative, and the authors must do more to quantify their findings and demonstrate how they improve upon inversions using lat-lon-pressure coordinates. I also question whether the analysis used is the best approach for testing their hypothesis. I have made specific line-by-line suggestions below.
Specific comments:
Lines 46-51: More information about the data exclusion process here is needed. Presumably these are being done to limit the dataset to those observations whose variance is dominated by synoptic-scale transport from the midlatitudes? How do the authors confirm their screening can “sufficiently reduce subtropical influence”? How do the results vary if these screening criteria are changed, and what recommendations can the authors make for other studies using this approach?
Lines 90-93: Please note which emission inventories were used rather than just referring to them as “default”. Also, please explain how the scaling factors for the ethane and propane emissions were derived. I think I found the details in Tribby et al. (2022)—they are related to observed ethane:propane ratios?-- but more information is needed here.
Line 99: While I see how some of variability across latitude is maybe collapsed when moving from pressure to potential temperature coordinates, the differences between Figure 2 and 3 are pretty subtle and I disagree with the authors’ claim that the curtain plots in Figure 3 look “very similar” at the different horizontal resolutions. A more quantitative comparison of the differences between simulations is warranted here.
Line 122-127 and Figure 4: A visual inspection is not sufficient here. Please provide some quantitative statistics to demonstrate good agreement between the simulations and aircraft data at all three horizontal resolutions and with the inclusions of the +/- 5 day window when using potential temperature as a coordinate. Also, please show how these statistics are improved relative to a comparison using lat-lon-pressure coordinates. Lastly, why was the 5-day time window chosen for comparison?
Line 137-150: This should all be moved to the Methods section rather than the Results.
Lines 151-158 and Table 1: This section needs the most additional work to be useful to the broader community. At the very least, it must include a comparison to inversions using lat-lon-pressure coordinates to prove that the resulting alpha is less dependent on model resolution when using potential temperature. Also, while the authors mention they did one test using the 4x5 degree simulated data as the observations in a 0.5x0.625 degree inversion, I question why the authors rely mostly on inversions using real observations rather than simulated ones in this analysis. It seems much easier to quantify the reliability of the results in the latter case, when the true flux is known and can be perturbed. Also, on that note, the authors need to address why the 95% credible interval is [0.71, 0.86] in the simulated inversion—shouldn’t it be approaching 1.0 in this case? I’m unclear if that’s the case for the inversion using real observations, but more discussion is needed to explain the behaviors here. Also, how dependent are the results on the spatial distribution of the emissions (i.e. if the authors used a prior with the same global flux but different spatial distribution)? Such a test would help demonstrate the limitations and applicability of this work in other contexts.
Technical comment:
Line 102: I think this should be referring to Figures S4-S7?
Citation: https://doi.org/10.5194/egusphere-2023-2227-RC2 -
AC2: 'Reply on RC2', Ariana Tribby, 13 Aug 2024
The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2023/egusphere-2023-2227/egusphere-2023-2227-AC2-supplement.pdf
-
AC2: 'Reply on RC2', Ariana Tribby, 13 Aug 2024
-
RC3: 'Referee comment on Tribby and Wennberg', Anonymous Referee #3, 31 Jan 2024
Tribby and Wennberg argue in “An analysis coordinate transform to facilite use of in-situ aircraft observations for flux estimation” that simulated ethane and propane fields from the GEOS-Chem transport model run at three different horizontal resolutions look similar when the chemical tracer is plotted on a latitude versus potential temperature coordinate, although they look different when plotted on a latitude versus pressure coordinate. They then conduct a simple optimization in which the simulated mole fractions are compared to observed mole fractions from the ATom campaign, at the same latitude and potential temperature, and scaled to match. Tribby and Wennberg report that the scale factor is within 10% for simulations whose resolution ranges from 4x5 deg to 0.5x0.625 deg. They use this agreement to conclude that the use potential temperature as the analysis coordinate for comparing simulated to observed tracers could save time and money associated with chemical transport modeling.
The analysis in the paper was insufficient to substantiate this conclusion, and major revisions and additional writing are required before the paper is suitable for publication.
There was no counterfactual presented, in terms of how close the optimization scale factors would be if a comparison were conducted in latitude/altitude space rather than latitude/potential temperature space. This comparison is critical to evaluate the authors’ conclusion about the benefits of the proposed coordinate transform.
There was no argument offered for the appropriate spatial resolution at which fluxes could be optimized. While the methods were not clear, I got the impression that the authors were optimizing fluxes uniformly or perhaps zonally, both of which would be coarser than what is desired for many chemical species. The authors do not show whether (or how) this approach could be used to improve flux optimizations at continental, regional, or local scales, where fluxes would be optimized on a 2-d grid rather than a zonal a.
The spatial scales of the chemical transport model were also coarse compared to that which would be desired for some applications (e.g., 10s of km), and it is not clear whether this approach would add value at those scales.
The authors simulate the chemical fields using fluxes that had previously been optimized in Tribby et al., 2022. Can this approach work when there are spatial biases in the distribution of prior fluxes fluxes (for example, zonal, meridional, or seasonal biases) imposed in the chemical transport model? If so, what are the limitations that are important for users of this approach to take into account?
The authors describe the results plotted in Fig. 3 as being more consistent across resolutions than those plotted in Fig. 2, although the results for February 23 look quite different among the three resolutions even in Fig. 3. On this day, there are elevated concentrations in isolated patches within the middle of the free troposphere apparent in the 0.5x0.625 deg simulation, but not in the other simulations. The ATom observations are not shown for this day, so it is not clear whether the elevated concentrations were observed or whether they are an artifact of the the transport model. In either case, the paper should discuss what characteristics of the meteorology on this day lead to the result that the potential temperature approach does not lead to convergence among the various resolutions.
In general, the paper read as incomplete. It is noteworthy that the paper did not have a Discussion or Conclusions section. This should be remedied before a revision is considered. It ends abruptly and leaves the reader with many questions, and it is surprising that the paper went out for review. The methods section lacked sufficient detail to understand the simulations and emissions inventories underlying the simulations. I am not familiar with Tribby et al., (2022), and relevant aspects of the methodology, results, and conclusions should be summarized briefly so that readers of this paper are not required to do an in-depth read of that paper. The results section did not contain the relevant analysis and documentation to substantiate the conclusioins (as described above), and the lack of discussion meant that it is not clear what the caveats of employing this method were.
Citation: https://doi.org/10.5194/egusphere-2023-2227-RC3 -
AC3: 'Reply on RC3', Ariana Tribby, 13 Aug 2024
The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2023/egusphere-2023-2227/egusphere-2023-2227-AC3-supplement.pdf
-
AC3: 'Reply on RC3', Ariana Tribby, 13 Aug 2024
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Ariana L. Tribby
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