the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 10 Nov 2023
Surface networks in the Arctic may miss a future "methane bomb"
Abstract. The Arctic is warming up to four times faster than the global average, leading to significant environmental changes. Given the sensitivity of natural methane (CH4) sources to environmental conditions, increasing Arctic temperatures are expected to lead to higher CH4 emissions, particularly due to permafrost thaw and the exposure of organic matter. Some estimates therefore assume an Arctic "methane bomb" where vast CH4 amounts are rapidly released. This study examines the ability of the in-situ observation network to detect such events in the Arctic, a generally poorly constrained region. Using the FLEXPART atmospheric transport model and varying CH4 emission scenarios, we found that areas with a dense observation network could detect a "methane bomb" in 2 to 10 years. In contrast, regions with sparse coverage would need 10 to 30 years, with potential false positives in other areas.
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Notice on discussion status
The requested preprint has a corresponding peer-reviewed final revised paper. You are encouraged to refer to the final revised version.
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Preprint
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The requested preprint has a corresponding peer-reviewed final revised paper. You are encouraged to refer to the final revised version.
- Preprint
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Supplement
(98 KB) - BibTeX
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- Final revised paper
Journal article(s) based on this preprint
Interactive discussion
Status: closed
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RC1: 'Comment on egusphere-2023-2308', Anonymous Referee #1, 12 Dec 2023
The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2023/egusphere-2023-2308/egusphere-2023-2308-RC1-supplement.pdf
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AC1: 'Reply on RC1', Sophie Wittig, 15 Mar 2024
The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2023/egusphere-2023-2308/egusphere-2023-2308-AC1-supplement.pdf
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AC1: 'Reply on RC1', Sophie Wittig, 15 Mar 2024
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RC2: 'Comment on egusphere-2023-2308', Mathias Göckede, 12 Dec 2023
Review on the manuscript titled ‘Surface networks in the Arctic may miss a future ‘methane bomb’, submitted for publication in Atmospheric Chemistry and Physics by Sophie Wittig and colleagues.
The authors present a study that aims at assessing what enhancement level of Arctic CH4 emissions may be reliably detected, and spatially attributed, based on GHG mixing ratio observations from the pan-Arctic tall tower network. Their approach uses atmospheric transport modeling with FLEXPART to first general synthetic time series of mixing ratios that reflect the changes in the atmosphere following surface flux enhancements at selected regions. In subsequent steps, these synthetic time series are then used as input for atmospheric inversions in an attempt to quantify, and spatially attribute, the surface flux rates of CH4 corresponding to the chosen emission scenarios. Since in this synthetic setup the ‘truth’ is known, this approach allows to quantify how well the inversion-based posterior fluxes agree with the true emissions, at what level of flux enhancement the higher fluxes are significantly different from the baseline, and how well the flux trends are assigned to the correct target regions. Based on these metrics, the authors conclude that substantial flux enhancements are required for a reliable detection, particularly in regions with sparse observations, and that a mis-attribution of the flux signals is quite common.
The overall objectives that Wittig et al. aim at are highly relevant – even in the absence of a ‘methane bomb’ scenario, enhanced GHG emission rates from degrading Arctic permafrost can be expected under future climate change, and a monitoring system that would reliably pick such changes would therefore be very useful. The in-situ atmospheric GHG monitoring tower network, in combination with atmospheric inverse modeling, is a suitable tool for this purpose, but due to the sparse network coverage the sensitivity of this tool towards future changes is still uncertain. The approach used within the context of this study, i.e. generating synthetic datasets with a known truth that allows to assess how well trends are quantified, and how reliable the spatial attribution of fluxes is, is well suited for this purpose. Unfortunately, some settings in the inversion setup seem to be over-simplified, so that even though the qualitative results may be solid, most quantifications are very questionable.
I see 3 major issues that compromise the findings presented in this work:
First, the authors produce synthetic mixing ratio observations as a prerequisite for conducting inversions for future emission scenarios, but they do not apply uncertainties when using this information in the actual inversions. Or rather, such uncertainties are not described in the presented paper, but based on the statement on p.11, ll.17-18 (These figures reflect an ideal case where uncertainties in the inversion system are minimized) I presume that none were applied. If this is the case, then the same transfer functions were applied in forward (to produce the synthetic data) and in backward modes (to execute the inversion). This is an over-simplification of the situation in a regular atmospheric inversion, where model-data mismatch uncertainties such as e.g. transport, mixing, or aggregation errors are a key component that make the links between surface processes and atmospheric observations much more challenging. Accordingly, all quantitative findings presented herein, such as years until detection of a change, or emission thresholds until detection, are highly questionable, and detection limits are likely low-biased.
Second, the fact that pan-Arctic posterior fluxes are systematically low-biased, compared to the ‘true’ fluxes in this synthetic experiment, suggest that the chosen setup is compromised. The best explanation I could come up with to interpret this phenomenon is that the correlation length scale chosen for FLEXPART does not allow to reproduce the steep gradients in regional flux patterns that emerge when emissions only in one region are ramped up extremely, while the neighboring regions stay at their low prior values. Such gradients obviously pose a major challenge to any inversion framework fed by sparse observations, where gaps in between monitoring sites need to be interpolated based on assumed spatial relationships within flux fields, necessarily producing (to a varying degree) smooth result surfaces. There may be other factors at play here, but emission peaks within target regions that are systematically underestimate, while adjacent regions have a high bias in fluxes, may be related to this. In any case, the problem requires further investigation, and in-depth discussion, both of which is currently lacking in this manuscript.
Third, I find several issues in the statistical measures used to evaluate flux trends:
- Equation (4) compares prior fluxes (in 2020) to posterior fluxes (in future years) and relates them to observational uncertainties to assign a detection limit. This calculation is only valid if prior and posterior fluxes in 2020 are exactly the same, for every target region. Since this study is based on synthetic data, there should not be a major adjustment between prior and posterior in the absence of a trend in emissions; however, since the observational network is sparse, there is reason to assume that prior and posterior are not identical even in 2020, which may lead to systematic difference even when aggregating fluxes by region. Without demonstrating that priors and posteriors are identical on a regional basis, the posterior fluxes in 2020 should be used as a reference (emis_b_2020), instead of the priors.
- Equation (5) compares ‘true’ to ‘posterior’ fluxes to quantify how much of the emission enhancement is actually captured by the inverse model. This is called ‘detected trend magnitudes’ in the section header, so the intention is obviously to quantify how much of the trend is captured. However, equation (5) compares absolute fluxes, not flux enhancements since 2020. For quantifying how much of the trend is actually captured by the inversion, I would find it more convincing to calculate how much the ‘true’ flux changed since 2020, and how much of a change is seen between the posterior fluxes over the same time span.
- I cannot really follow the logic behind equation (6), even though the objective to quantify mis-attribution is highly relevant. Why is the ‘delta_emis’ measure used here? The authors state themselves in Section 4.2.2 that a good ‘delta_emis’ factor, i.e. with a value close to zero, indicates that the posterior is very close to the true emissions. Now when dividing the sum of ‘delta_emis’ in other regions by the ‘delta_emis’ from the study region, if the latter value is close to zero the result would be rather high increment ratios ..?? So why use the ‘delta’ measure in the first place here? I would find it much more intuitive if the authors first quantify how much integrated pan-Arctic flux budgets were increased when raising fluxes in a single region, i.e. how much of that ‘true’ signal is actually detected by the inversion, no matter where exactly. Next, you should simply quantify what fraction of that enhancement is attributed to the target region where fluxes were enhanced, and what fraction lies outside.
Linked to the above shortcomings, I find all quantitative results presented in this manuscript highly uncertain, and in part questionable. As a consequence, the conclusions drawn are not really supported by the results presented. All of this, however, should be possible to be upgraded for a revised version of this study. Since I see a high relevance in the general target of this study, and would thus like to see it published, I would, very cautiously, recommend to accept this material for publication in ACP, but only if the above-mentioned major issues have been taken care of.
Additional comments:
- I don’t find the flow charts (Figs. 1, 4) too helpful in the current format.
- Using emissions, or emission thresholds, in absolute numbers (e.g. Tg/yr) is misleading, since the size of the regions is variable, and unknown to the reader. Fluxes would be more intuitive if normalized by area.
- When presenting the ‘inversion method’ as Section 2, some details are missing. Maybe it would be better to place this after the ‘material’ section.
- In Section 3.2, definitions are not ‘clean’, since the assumption of continuous data everywhere already upgrades the ‘current’ network. Also, some more details on the networks, e.g. total number of sites, or regional distribution, should be added to the text.
- In Section 3.4, more information on the setup of FLEXPART and the optimization strategy would be helpful.
Citation: https://doi.org/10.5194/egusphere-2023-2308-RC2 -
AC2: 'Reply on RC2', Sophie Wittig, 15 Mar 2024
The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2023/egusphere-2023-2308/egusphere-2023-2308-AC2-supplement.pdf
Interactive discussion
Status: closed
-
RC1: 'Comment on egusphere-2023-2308', Anonymous Referee #1, 12 Dec 2023
The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2023/egusphere-2023-2308/egusphere-2023-2308-RC1-supplement.pdf
-
AC1: 'Reply on RC1', Sophie Wittig, 15 Mar 2024
The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2023/egusphere-2023-2308/egusphere-2023-2308-AC1-supplement.pdf
-
AC1: 'Reply on RC1', Sophie Wittig, 15 Mar 2024
-
RC2: 'Comment on egusphere-2023-2308', Mathias Göckede, 12 Dec 2023
Review on the manuscript titled ‘Surface networks in the Arctic may miss a future ‘methane bomb’, submitted for publication in Atmospheric Chemistry and Physics by Sophie Wittig and colleagues.
The authors present a study that aims at assessing what enhancement level of Arctic CH4 emissions may be reliably detected, and spatially attributed, based on GHG mixing ratio observations from the pan-Arctic tall tower network. Their approach uses atmospheric transport modeling with FLEXPART to first general synthetic time series of mixing ratios that reflect the changes in the atmosphere following surface flux enhancements at selected regions. In subsequent steps, these synthetic time series are then used as input for atmospheric inversions in an attempt to quantify, and spatially attribute, the surface flux rates of CH4 corresponding to the chosen emission scenarios. Since in this synthetic setup the ‘truth’ is known, this approach allows to quantify how well the inversion-based posterior fluxes agree with the true emissions, at what level of flux enhancement the higher fluxes are significantly different from the baseline, and how well the flux trends are assigned to the correct target regions. Based on these metrics, the authors conclude that substantial flux enhancements are required for a reliable detection, particularly in regions with sparse observations, and that a mis-attribution of the flux signals is quite common.
The overall objectives that Wittig et al. aim at are highly relevant – even in the absence of a ‘methane bomb’ scenario, enhanced GHG emission rates from degrading Arctic permafrost can be expected under future climate change, and a monitoring system that would reliably pick such changes would therefore be very useful. The in-situ atmospheric GHG monitoring tower network, in combination with atmospheric inverse modeling, is a suitable tool for this purpose, but due to the sparse network coverage the sensitivity of this tool towards future changes is still uncertain. The approach used within the context of this study, i.e. generating synthetic datasets with a known truth that allows to assess how well trends are quantified, and how reliable the spatial attribution of fluxes is, is well suited for this purpose. Unfortunately, some settings in the inversion setup seem to be over-simplified, so that even though the qualitative results may be solid, most quantifications are very questionable.
I see 3 major issues that compromise the findings presented in this work:
First, the authors produce synthetic mixing ratio observations as a prerequisite for conducting inversions for future emission scenarios, but they do not apply uncertainties when using this information in the actual inversions. Or rather, such uncertainties are not described in the presented paper, but based on the statement on p.11, ll.17-18 (These figures reflect an ideal case where uncertainties in the inversion system are minimized) I presume that none were applied. If this is the case, then the same transfer functions were applied in forward (to produce the synthetic data) and in backward modes (to execute the inversion). This is an over-simplification of the situation in a regular atmospheric inversion, where model-data mismatch uncertainties such as e.g. transport, mixing, or aggregation errors are a key component that make the links between surface processes and atmospheric observations much more challenging. Accordingly, all quantitative findings presented herein, such as years until detection of a change, or emission thresholds until detection, are highly questionable, and detection limits are likely low-biased.
Second, the fact that pan-Arctic posterior fluxes are systematically low-biased, compared to the ‘true’ fluxes in this synthetic experiment, suggest that the chosen setup is compromised. The best explanation I could come up with to interpret this phenomenon is that the correlation length scale chosen for FLEXPART does not allow to reproduce the steep gradients in regional flux patterns that emerge when emissions only in one region are ramped up extremely, while the neighboring regions stay at their low prior values. Such gradients obviously pose a major challenge to any inversion framework fed by sparse observations, where gaps in between monitoring sites need to be interpolated based on assumed spatial relationships within flux fields, necessarily producing (to a varying degree) smooth result surfaces. There may be other factors at play here, but emission peaks within target regions that are systematically underestimate, while adjacent regions have a high bias in fluxes, may be related to this. In any case, the problem requires further investigation, and in-depth discussion, both of which is currently lacking in this manuscript.
Third, I find several issues in the statistical measures used to evaluate flux trends:
- Equation (4) compares prior fluxes (in 2020) to posterior fluxes (in future years) and relates them to observational uncertainties to assign a detection limit. This calculation is only valid if prior and posterior fluxes in 2020 are exactly the same, for every target region. Since this study is based on synthetic data, there should not be a major adjustment between prior and posterior in the absence of a trend in emissions; however, since the observational network is sparse, there is reason to assume that prior and posterior are not identical even in 2020, which may lead to systematic difference even when aggregating fluxes by region. Without demonstrating that priors and posteriors are identical on a regional basis, the posterior fluxes in 2020 should be used as a reference (emis_b_2020), instead of the priors.
- Equation (5) compares ‘true’ to ‘posterior’ fluxes to quantify how much of the emission enhancement is actually captured by the inverse model. This is called ‘detected trend magnitudes’ in the section header, so the intention is obviously to quantify how much of the trend is captured. However, equation (5) compares absolute fluxes, not flux enhancements since 2020. For quantifying how much of the trend is actually captured by the inversion, I would find it more convincing to calculate how much the ‘true’ flux changed since 2020, and how much of a change is seen between the posterior fluxes over the same time span.
- I cannot really follow the logic behind equation (6), even though the objective to quantify mis-attribution is highly relevant. Why is the ‘delta_emis’ measure used here? The authors state themselves in Section 4.2.2 that a good ‘delta_emis’ factor, i.e. with a value close to zero, indicates that the posterior is very close to the true emissions. Now when dividing the sum of ‘delta_emis’ in other regions by the ‘delta_emis’ from the study region, if the latter value is close to zero the result would be rather high increment ratios ..?? So why use the ‘delta’ measure in the first place here? I would find it much more intuitive if the authors first quantify how much integrated pan-Arctic flux budgets were increased when raising fluxes in a single region, i.e. how much of that ‘true’ signal is actually detected by the inversion, no matter where exactly. Next, you should simply quantify what fraction of that enhancement is attributed to the target region where fluxes were enhanced, and what fraction lies outside.
Linked to the above shortcomings, I find all quantitative results presented in this manuscript highly uncertain, and in part questionable. As a consequence, the conclusions drawn are not really supported by the results presented. All of this, however, should be possible to be upgraded for a revised version of this study. Since I see a high relevance in the general target of this study, and would thus like to see it published, I would, very cautiously, recommend to accept this material for publication in ACP, but only if the above-mentioned major issues have been taken care of.
Additional comments:
- I don’t find the flow charts (Figs. 1, 4) too helpful in the current format.
- Using emissions, or emission thresholds, in absolute numbers (e.g. Tg/yr) is misleading, since the size of the regions is variable, and unknown to the reader. Fluxes would be more intuitive if normalized by area.
- When presenting the ‘inversion method’ as Section 2, some details are missing. Maybe it would be better to place this after the ‘material’ section.
- In Section 3.2, definitions are not ‘clean’, since the assumption of continuous data everywhere already upgrades the ‘current’ network. Also, some more details on the networks, e.g. total number of sites, or regional distribution, should be added to the text.
- In Section 3.4, more information on the setup of FLEXPART and the optimization strategy would be helpful.
Citation: https://doi.org/10.5194/egusphere-2023-2308-RC2 -
AC2: 'Reply on RC2', Sophie Wittig, 15 Mar 2024
The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2023/egusphere-2023-2308/egusphere-2023-2308-AC2-supplement.pdf
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Sophie Wittig
Antoine Berchet
Isabelle Pison
Marielle Saunois
Jean-Daniel Paris
The requested preprint has a corresponding peer-reviewed final revised paper. You are encouraged to refer to the final revised version.
- Preprint
(5658 KB) - Metadata XML
-
Supplement
(98 KB) - BibTeX
- EndNote
- Final revised paper