Improved estimates on global carbon stock and carbon pools in tidal wetlands

Tidal wetlands are global hotspots of carbon storage but errors exist with current estimates on their carbon density due to the use of factors estimated from other habitats for converting loss-on-ignition (LOI) to organic carbon (OC); and the omission of certain significant carbon pools. Here we show that the widely used conversion factor (LOI/OC = 1.724) is significantly lower than our measurements for saltmarsh sediments (1.92 ± 0.01) and oversimplifies the polynomial relationship between sediment OC and LOI for mangrove forests. Global mangrove OC stock in the top-meter sediment reaches 1.93 Pg when corrected for this bias, and is 20% lower than the previous estimates. Ecosystem carbon stock (living and dead biomass, sediment OC and inorganic carbon) is estimated at 3.7–6.2 Pg. Mangrove deforestation leads to carbon emission rates at 23.5–38.7 Tg yr−1 after 2000. Mangrove sediment OC stock has previously been over-estimated while ecosystem carbon stock underestimated.

The second argument, that underreporting carbonate stock leads to an underreporting of total stock. This may be true; I think this is missing important context. The process of forming and trapping of carbonates can have a net-warming or cooling effect depending on where carbonates were generated and what the scope of the analysis is (Howard; Lu). In some cases, long-term carbonate formation reverses cooling trend of organic carbon burial. This is an essential piece of context on the connection between formation rates, observed stocks, and net greenhouse gas balance that I did not see anywhere in the manuscript.
The third argument, that stocks are underreported because they do not include dead wood I think was also a bit weak. I never saw any citations or summary statistics indicating how many studies lacked dead wood, or how many included it. I know that there is guidance for accounting for dead wood in the IPCC wetland supplement guidance. I can also think of a few studies off the top of my head that do include it, although they tend to be tidal freshwater forested literature (Megonigal 1997;Krauss et al., 2018). Maybe there's a hole in the mangrove literature I'm not aware of that could be communicated better than answered by this point.
If the editors decide to seek a revised manuscript, I have some suggestions below.
Overall. 1. The authors claim that saltmarshes and mangroves have different OM to OC ratios. If they think this is the result of a biological mechanism, I would like this explored more in the discussion. Also, could be that this is an artifact of the data synthesis. This could be addressed by trying a mixedeffects model, the same model as is done here with a 'study level' random effect. 2. Figures -Figure 1. The log transformation makes the 95% CI's look like their exactly on the median line. There is missing symbology in the equations. The images are unnecessary. The top figure has log-transformed axes and the bottom they are linear. This is misleading and implies that the two relationships have more similar fits than they actually do. I recommend putting them on the same comparable axes and adding the 0.58 gOC per gOM line in for comparison. 3. I suggest a more thoughtful use of color. The color schemes for figures 2 and 4 are the same, but the colors mean different things. I suggest changing the palates in one or both. 4. The histogram in fig. 2 doesn't really communicate the fact that there are significant differences in carbon stocks between latitudinal clusters to me. The variance in carbon stocks at different latitudinal gradients seems interesting and maybe deserves more attention in the main text. 5. SI table -There is a lot of unpublished data listed, and I would like to see any personal communications or submitter contact information cited in SI. 6. I suggest a column indicating the precision (number of decimal points) appropriate for the latlong's. 7. I suggest machine-readable and analysis-ready datasets for everything they've produced in house (Wilson et al 2017;Culina et al 2018). I also suggest adopting the hierarchical set of site, core, depth series table format reccomended by the Coastal Carbon Research Coordination Network (https://serc.si.edu/coastalcarbon/database-structure#site-level).
Line comments.
Line 62: Is the site, the core, or the depth interval the fundamental unit of the analysis? I think depth interval is best.
Line 71: I'd prefer a more precise or quantitative phrase than 'clear cut'.
Line 73: Somewhere in the results section it would be good to say how many significance tests were run, how independent they were. Consider running a Bonferroni correction to p-values to account for multiple testing.
Line 76-78: The claim is that 0.58 gOC per gOM is adopted by most studies. I haven't seen any evidence for this in the paper. In the SI it seems like a small subset of 13 studies.
Also when reporting the regression equations, the authors should add the standard error of the parameter estimates.
I think something more rigorous is needed than dropping a parameter because it is not significantly different from one. I suggest comparing a linear and polynomial versions of the model fit separately using Akaike's Information Criterion.
Were salt marsh and mangrove relationships fit separately, or were they fit using the same model and an ecosystem type fixed effect?
Line 80-89: How does this compare with Rogers et al 2019, who found that carbon stocks were higher in the regions where there was more historical isostatic sea-level rise forming accommodation space?
Line 96: Would this still be significant after adjusting for multiple testing?
Line 102: I think this sentence should be in the abstract.
Was it the correction of past studies using the 0.58 gOC per gOM or the switch from reporting means to medians which caused the 24% drop in total estimated stocks?
Materials and methods -I could use more details regarding the scenarios depicted in Fig. 4. I did not see them referenced in the main text at all and when I finished reading the paper I did not have a good idea as to where they came from and how they fit into the research questions. Culina, A. et al., 2018. Navigating the unfolding open data landscape in ecology and evolution. Nature Ecology & Evolution, pp.1-7.
Reviewer #3 (Remarks to the Author): Overall I found the manuscript to contain material that would be a worthwhile contribution to the literature with several innovative elements. My criticisms are broad in nature, so I have not provided line-by-line comments. My primary criticism is that it was unclear whether the goal of this manuscript was to critique and suggest improvements for factors to convert loss-on-ignition (LOI) to organic carbon (OC) or to provide an updated global mangrove C stock estimate. In its current form, the manuscript attempts to do both, but the combination of these separate goals created many weaknesses and elements of confusion. As one example, it was confusing whether the updated global C stock estimates were a result of the different conversion factors, or the new data collected, or other reasons. I recommend splitting the manuscript into two. A manuscript that were to establish improved conversion factors that potentially could be used throughout the scientific community would be a highly valuable contribution to the literature and could include an implications section on how this may affect global stock estimates. A manuscript on new global-stock mangrove carbon estimates, using these new conversion factors and other new data, would also be a highly valuable contribution to the literature. Both of these contributions are sufficiently important in scope to warrant their own publication and a more comprehensive and focused treatment.
For the conversion factors paper, I suggest adding: -A clear and comprehensive review of conversion factors that have been developed in the literature.
-A similar review of how these conversion factors have been applied. A table summarizing these uses would be very helpful. This could be restricted to global C stock estimates, but could also be highly valuable if it covers C stock estimates at other scales. The use of conversion factors is far broader in scope than just for global C stock estimates.
For global mangrove C carbon stock estimates, I suggest adding: -A clear and comprehensive review of previous global mangrove C stock estimates and how and why they differ from the present study. A table would be useful.
Additional broad criticisms: -The manuscript focuses on the role of coastal wetlands in mitigating climate change, but then criticizes previous studies for not including inorganic C in C stock estimates. Inorganic C is of course a component of the total C pool of a wetland, but is far less dynamic than organic C and probably plays little role in the ecosystem service of greenhouse gas mitigation. For this reason, it seems best to separate these pools when doing C stock estimates as a means to understand greenhouse gas mitigation.
-Also related to greenhouse gas mitigation is the issue of human alterations. There is a substantial difference in terms of understanding climate forcing in quantifying C stocks and quantify C stock changes resulting from human activities. This separation is generally not made clear in the manuscript.
-The carbon stock estimate was only for mangroves, but the conversion factors were for both mangroves and marshes, which was confusing and not made clear in the paper. This is another reason to split the paper. -There are quite a few comments such as the one on line 35 "but has been ignored in current estimates" without references. See lines 39¬-40 and 76 as other examples, but there are others as well. This would be remedied by have a more comprehensive analysis of conversion factors in the literature.
-The manuscript is written as if the 1.724 LOI/OC ratio is essentially the only one that has been used in the literature, but this is incorrect -there are many examples of other ratios that have been used. In fact, in a recent important publication this isn't the ratio that is suggested for use in mangroves (see Table 3 -The authors state on line 77 that the polynomial relationship was not statistically significant, but do not explain/defend why it was then used. -The manuscript is written as if the new data that were collected were global in nature, but only in the methods is it clarified that all of these data come from China (I believe). There is nothing wrong with adding data from China to this global database, but it should be explicit throughout the manuscript. It should also be discussed about whether these data fill a data gap-was China and/or these wetland types a data gap? Is this new database in any way weighted with the large number of samples from China? -The use of the term "correct" should be replaced with something like "improve". As scientists, we will never have the "correct" answer for a statistical population.
I should note that although I have expertise in wetland soil carbon cycling, I don't have expertise in global-scale carbon stock estimation, so I was not able to critique this element of the manuscript.

Reviewer #1 Overall comments
They find strong relationships (as shown before), but which have different slopes to those reported earlier in the literature, reflecting the growing number of studies from a wider range of study sites. They use these relationships (although they use two different equations for mangroves, for Low and high OC sites, which is not clear in the main text, but appears in the supplementary) to re-estimate the OC stocks in mangroves The previous published estimates on the relationship were either studies on specific sites or global analyses of database with limited coverage (Supplementary Information Table 3). We have developed relationships based on an expanded database from our synthesis and additional original field measurements, which cover both the Indo-west-Pacific and Atlantic-east-Pacific biogeographic regions. With growing interest in blue carbon, our evaluation of the conversion factor is timely as well as important. We presented a revised and different relationship between OC and LOI based on all collated mangrove data in the main text of the manuscript as this is critical to improving future estimates of OC from LOI. We further explain why we developed the relationships for low and high LOI sediments in the Supplementary Information.

Supplementary
Information Table  3, l. 186-188, Supplementary  Information Specific comments 1. The statement that there is a "universal conversion factor" suggests that all blue carbon stock assessments use this factor when this is not the case. Additionally, there is no reference provided for this statement.
We have revised this sentence to avoid overstating the use of a single conversion factor. l. 10, l. 34, l. 37 2. That mangrove carbon stock assessments "ignore" inorganic carbon stocks is overstated. As the data set presented shows, in most mangrove ecosystems inorganic carbon is very low and may not be reported because preliminary measures find it is low (usually reported in methods), unless it is of particular interest (e.g. see Xiong et al. 2019, Biology Letters).
Sediment inorganic carbon is assumed to be less important in many references. However, we found globally sediment IC contributes 14.6% of sediment OC stock, and therefore include it as a component of sediment carbon stocks in our discussion, which is another contribution of our study. Actually, sediment l. 151-157, l. 54-57 IC can have a warming or cooling effect depending on the formation process (Refer to our later response to Reviewer #2's comment on argument 2). 3. "Young sediments" -are these sediments recently colonized by intertidal plant communities?
The reference did not explain this point and we have rephrased the sentence to avoid confusion.
l. 44-46 4. This statement: "Nevertheless, their OC:LOI ratios are largely unknown, and even if measured, are not differentiated from other organic-rich sediments when estimating OC from organic matter by the LOI method." Is rather sweeping with no reference to indicate where this is the case.
We have added a reference related to this issue in the revised manuscript.
l. 52 5. The statement: "incorporating the representative values of individual sediment OC stocks." meaning was not clear.
We have revised this sentence to improve clarity l. 66-67 6. The polynomial term for mangrove LOI-OC was not significant, so the relationship should not be reported as polynomial.
In the first version of the manuscript, we stated that 'the exponent (1.02) of the polynomial relationship was insignificantly different from 1' which does not mean the polynomial model for mangrove LOI-OC was not significant. It just means the polynomial relationship can be approximated by the linear relationship. In the revised ms, we have improved the relationship with more data and now the exponent is different from 1, i.e. the polynomial relationship cannot be approximated by a linear relationship. With more data on sediment IC, we found that the median value is representative of global mangrove sediment IC stocks, and replaced the geometric mean in the ms. We also provide the mean value of sediment IC stocks. We have discussed the likely high IC in karstic environments and Holocene reef tops, citing the relevant references. global relationship using available data from past studies and our new field data.
We agree that the van Baemmelen factor (OC:LOI=0.58) is too high for wetland sediments while Craft (1991) was developed from marsh sediments from a few sites in USA. The new relationship we developed is an advancement over the past relationships because we include (1) separate relationships for mangroves and saltmarshes; (2) data from coastal wetlands covering both the Indo-west-Pacific and Atlantic-east-Pacific biogeographic regions. 2. The second argument, that underreporting carbonate stock leads to an underreporting of total stock. This may be true; I think this is missing important context. The process of forming and trapping of carbonates can have a net-warming or cooling effect depending on where carbonates were generated and what the scope of the analysis is (Howard; Lu). In some cases, longterm carbonate formation reverses cooling trend of organic carbon burial. This is an essential piece of context on the connection between formation rates, observed stocks, and net greenhouse gas balance that I did not see anywhere in the manuscript.
We have briefly clarified the biogeochemical process of sediment inorganic carbon deposition associated with calcifying organisms and dissolution, which may have a warming or cooling effect dependent on the formation processes of inorganic carbon in different coastal ecosystems, e.g. seagrasses and chenier plains, citing the relevant references.
l. 54-57 3. The third argument, that stocks are underreported because they do not include dead wood I think was also a bit weak. I never saw any citations or summary statistics indicating how many studies lacked dead wood, or how many included it. I know that there is guidance for accounting for dead wood in the IPCC wetland supplement guidance. I can also think of a few studies off the top of my head that do include it, although they tend to be tidal freshwater forested literature (Megonigal 1997;Krauss et al., 2018) have included these references in our dataset on dead wood biomass carbon. Overall comments 1. The authors claim that saltmarshes and mangroves have different OM to OC ratios. If they think this is the result of a biological mechanism, I would like this explored more in the discussion. Also, could be that this is an artefact of the data synthesis. This could be addressed by trying a mixed-effects model, the same model as is done here with a 'study level' random effect.
We have provided a possible mechanism explaining the difference in relationships between mangrove and saltmarsh OC and LOI. The LOI data can have laboratory specific biases since our data are a combination of synthesised data from multiple sources and our field data. The individual study (i.e. 'study level') can be a random factor in the model, similar to Holmquist (2018). More importantly, however, the ranges of LOI and OC for individual studies of the two ecosystem types are also different without overlapping (Supplementary Information  Table 1). So the random effect of individual data is already considered in the regression equations. From this point of view, the inclusion of 'study level' as a separate random effect could not explain the specific biases from different laboratories and is not considered in our revision.
l. 188-198 2. Figures -Figure 1. The log transformation makes the 95% CI's look like their exactly on the median line. There is missing symbology in the equations. The images are unnecessary. The top figure has log-transformed axes and the bottom they are linear. This is misleading and implies that the two relationships have more similar fits than they actually do. I recommend putting them on the same comparable axes and adding the 0.58 gOC per gOM line in for comparison.
We have used the same axes for both regression relationships but not in one figure since the large amount of data points will obscure which ones come from mangroves or saltmarshes. The missing symbol is due to transformation of word to pdf document in the online submission system and we will avoid the problem in the revised submission. We have also added the line with the slope of 0.58 (OC/OM) for comparison. Fig. 1 3. I suggest a more thoughtful use of color. The color schemes for figures 2 and 4 are the same, but the colors mean different things. I suggest changing the palates in one or both.
We have used another colour scheme for Fig. 2. Fig. 2 4. The histogram in fig. 2 doesn't really communicate the fact that there are significant differences in carbon stocks between latitudinal clusters to me. The variance in carbon stocks at different latitudinal gradients seems interesting and maybe deserves more attention in the main text.
The histogram in fig.2 (fig.2a) just shows the distribution of sediment carbon stock at various latitudinal ranges. The difference is shown in fig.2b and the K-W chi-square value is added. We have made it clear that the significant difference in carbon stocks can be observed in fig.2b rather than fig.2. l. 104 5. SI table -There is a lot of unpublished data listed, and I would like to see any personal communications or submitter contact information cited in SI.
We have indicated the unpublished data coming from Atwood et al. (2017) in the Supplement Dataset.

Supplementary
Dataset on carbon references 6. I suggest a column indicating the precision (number of decimal points) appropriate for the lat-long's.
We have added two columns indicating the precision for the latitudes and longitudes.

Supplementary
Dataset on sites, cores and depths 7. I suggest machine-readable and analysis-ready datasets for everything they've produced in house (Wilson et al 2017;Culina et al 2018). I also suggest adopting the hierarchical set of site, core, depth series table format reccomended by the Coastal Carbon Research Coordination Network (https://serc.si.edu/coastalcarbon/database-structure#sitelevel).
We have prepared the datasets that are ready for analysis. The dataset on sediment OC stock has been supplemented with the hierarchical set of site, core and depth series, including study and core ID, core elevation, salinity code, vegetation code, inundation code, core length, minimum and maximum core depth, and relative sea level rise over the late Holocene zones. We have also provided other Supplementary datasets.

Specific comments
Line 62: Is the site, the core, or the depth interval the fundamental unit of the analysis? I think depth interval is best.
We have provided depth intervals in the Supplementary Dataset on sediment OC.

Supplementary
Dataset on sites, cores and depths Line 71: I'd prefer a more precise or quantitative phrase than 'clear cut'.
We have replaced the phrase but not a quantitative one because the polynomial and linear relationships cannot be compared quantitatively.

l. 88
Line 73: Somewhere in the results section it would be good to say how many significance tests were run, how independent they were. Consider running a Bonferroni correction to pvalues to account for multiple testing.
We have run the Bonferroni correction to P values for multiple tests here and hereafter.
l. 89-90, l. 128-130, l. 328-330 Line 76-78: The claim is that 0.58 gOC per gOM is adopted by most studies. I haven't seen any evidence for this in the paper. In the SI it seems like a small subset of 13 studies. Also when reporting the regression equations, the authors should add the standard error of the parameter estimates. I think something more rigorous is needed than dropping a parameter because it is not significantly different from one. I suggest comparing a linear and polynomial versions of the model fit separately using Akaike's Information Criterion. Were salt marsh and mangrove relationships fit separately, or were they fit using the same model and an ecosystem type fixed effect?
We have modified the sentence to avoid misunderstanding. Standard errors of the parameter estimates have been added when reporting the regression equations. The polynomial term is significantly different from one and the exponent is not dropped after further updating the dataset on mangrove OC and LOI. So the linear relationship cannot be used to approximate the polynomial relationship for mangroves. We have clarified that the relationships for saltmarshes and mangroves were fitted separately.

Supplementary
Information, text and Table 3 , l. 96-98, l. 64 Line 80-89: How does this compare with Rogers et al 2019, who found that carbon stocks were higher in the regions where there was more historical isostatic sea-level rise forming accommodation space The latitudinal change in sediment OC stocks is not comparable with the data in Rogers et al. 2019, but we supplement the variation of sediment OC stocks with relative sea level rise over the late Holocene zones, and found it consistent with the reference.
l. 111-116 Line 96: Would this still be significant after adjusting for multiple testing?
Yes. It is still significant after the Bonferroni correction.
l. 136 Line 102: I think this sentence should be in the abstract. Was it the correction of past studies using the 0.58 gOC per gOM or the switch from reporting means to medians which caused the 24% drop in total estimated stocks?
The information is shown in the abstract. The drop in the total estimated OC stock is mainly due to the switch from reporting means to medians, which is statistically more desirable to avoid the undue effect of extreme values. Other factors also result in the difference, including the different conversion factors used, the number of studies (147 studies in the previous synthesis and 235 studies in ours).
l. 16, l. 204-213 Materials and methods -I could use more details regarding the scenarios depicted in Fig. 4. I did not see them referenced in the main text at all and when I finished reading the paper I did We have described in more detail about the different scenarios in Fig.4. l. 338-341 not have a good idea as to where they came from and how they fit into the research questions. Reviewer #3 Overall comments 1. My primary criticism is that it was unclear whether the goal of this manuscript was to critique and suggest improvements for factors to convert loss-on-ignition (LOI) to organic carbon (OC) or to provide an updated global mangrove C stock estimate. In its current form, the manuscript attempts to do both, but the combination of these separate goals created many weaknesses and elements of confusion. As one example, it was confusing whether the updated global C stock estimates were a result of the different conversion factors, or the new data collected, or other reasons. I recommend splitting the manuscript into two.
We have reiterated in the ms that it is necessary to improve factors to convert OC from LOI due to (1) the wide use of conversion factors (e.g. 0.58) in individual case studies to estimate OC from LOI, and (2) the previous global estimates on sediment OC stock are based on conversion factors estimated from samples from single mangrove sites or non-mangrove habitats. This will partly, if not entirely, bias the estimate on global sediment OC stocks in mangroves. Thus, it is necessary to obtain a conversion factor based on global data before the global estimate of sediment OC stock may be improved. The difference between our estimated global C stock and previous estimates is attributed to (1) the corrected conversion factors; (2) new data collected; and (3) a full inventory of carbon pools, as explained in response to Reviewer #2's specific comment above. The messages are strongly interrelated and we therefore prefer to keep both objectives in one ms.
l. 37-44, l. 204-213 2. I suggest adding: a clear and comprehensive review of conversion factors that have been developed in the literature. A similar review of how these conversion factors have been applied. A table summarizing these uses would be very helpful. This could be restricted to global C stock estimates, but could also be highly valuable if it covers C stock estimates at other scales. The use of conversion factors is far broader in scope than just for global C stock estimates.
We have added a table listing published conversion factors for coastal wetlands in the Supplement Information. Please also refer to our response to this point in the reply to Reviewer #2' comment above. Table  3, l. 180-201 3. For global mangrove C carbon stock estimates, I suggest adding: A clear and comprehensive review of previous global mangrove C stock estimates and how and why they differ from the present study. A table would be useful.

Supplementary Information
We have added a table listing previous global mangrove C stock estimates, and compare them with our results. Table 1 Additional comments The manuscript focuses on the role of coastal wetlands in mitigating climate change, but then criticizes previous studies for not including inorganic C in C stock estimates. Inorganic C is of course a component of the total C pool of a wetland, but is far less dynamic than organic C and probably plays little role in the ecosystem service of greenhouse gas mitigation. For this reason, it seems best to separate these pools when doing C stock estimates as a means to understand greenhouse gas mitigation.
We have highlighted the different nature of sediment OC and IC. Our result found that sediment IC is 14.6% of sediment OC stock, and is an important component of ecosystem carbon stock in mangroves. It may still have warming or cooling effect depending on the formation process (refer to our response to Reviewer #2's comment on argument 2). With other changes such as warming and ocean acidification affecting this component, we feel it necessary to include IC in our analysis.
l. 54-60, l. 151-153 Also related to greenhouse gas mitigation is the issue of human alterations. There is a substantial difference in terms of understanding climate forcing in quantifying C stocks and quantify C stock changes resulting from human activities. This separation is generally not made clear in the manuscript.
We have discussed the impact of climate on mangrove C stocks. Refer to our response to Reviewer #1's specific comment 9.
l. 231-237 The carbon stock estimate was only for mangroves, but the conversion factors were for both mangroves and marshes, which was confusing and not made clear in the paper.
We have further clarified this in the revised ms.
l. 64-65 There are quite a few comments such as the one on line 35 "but has been ignored in current estimates" without references. See lines 39-40 and 76 as other examples, but there are others as well. This would be remedied by have a more comprehensive analysis of conversion factors in the literature. The manuscript is written as if the 1.724 LOI/OC ratio is essentially the only one that has been used in the literature, but this is incorrect -there are many examples of other ratios that This comment has been addressed along with this Reviewer's overall comment 2 and Reviewer #2's comment on argument 1.
The different LOI/OC or OC/LOI ratios are compared with our study in a table, as stated above.