the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 10 Nov 2023
Spectroscopic assessment of three ecologically distinct organic carbon fractions of mineral soils
Abstract. Soil carbon (C) is heterogeneous and exists in various forms along a decomposition continuum from labile fast-cycling compounds to more persistent forms of C, which can reside in the soil for centuries to millennia. Methods for soil organic C fractionation aim to account for this complexity by separating soil organic C into distinct groups that exhibit similar turnover. Our aims were to (a) fractionate three mineral soils with small C concentrations (<2.5 % C), different textures and mineralogy using a granulometric method to derive the particulate organic C in macroaggregates (POCmac), the particulate organic C in microaggregates (POCmic), and the mineral-associated organic carbon (MAOC), (b) test if mid-infrared (MIR) spectra can discriminate the distinct organic C fractions and characterise the critical organic and mineral functional groups, and c) explore the interactions between the dominant mineral and organic functional groups to elucidate C stabilisation. With a multivariate analyses we found that the MIR spectra use information from mineral and organic frequencies to discriminate the organic C fractions. Closer investigation on specific regions of the MIR spectrum showed that absorptions relating to silicates were more pronounced in the POCmac and POCmic fractions and clay mineral absorptions were stronger in the MAOC fraction. There was little organic C in the POCmic and POCmac fractions, respectively, and their spectra showed mostly mineralogical features. Most of the organic C in the soils was present as MAOC. The stretching vibration of the bonds in the alkyl CH2 molecule was most prominent. However, absorptions from C = C and C = O stretching vibrations, due to alkenes and amides were also present. These molecules are known to form MAOC. We found that the wavenumbers associated with the absorption of alkyl CH2 were positively correlated with the absorption of clay minerals, which may be used to infer the mineral association of organic C. Our results show that MIR spectroscopy can characterise the compositional differences between the C fractions and that the spectra could potentially infer C stabilisation in mineral soils.
- Preprint
(8814 KB) - Metadata XML
-
Supplement
(1023 KB) - BibTeX
- EndNote
Status: closed
-
RC1: 'Comment on egusphere-2023-2464', Anonymous Referee #1, 19 Dec 2023
Review for manuscript egusphere-2023-2464 for the journal Soil by Walden et al.
The manuscript describes the results of an MIR based spectroscopic analyses of three size-based soil organic matter fractions in low C-soils of Australia of varying texture and to test whether MIR spectra can discriminate between mineral and organic functional groups and explore relationships between them.
With this focus, the manuscript deals with an important topic that is worth exploring and could certainly provide insights that would help to close data gaps across soil types with respect to carbon storage, stabilization mechanisms and (potentially) carbon turnover. I do think however that the manuscript falls short at several occasions to provide what is to be expected from these objectives and the finally delivered novelty of the analyses is unclear to me.
My main concerns:
- The title speaks of “ecologically distinct” organic carbon fractions, but it remains unclear what this means for the authors. The applied fractionation scheme isolates size classes and not functional pools or fractions. In fact, the terms used in the manuscript (labeling the fractions >50µm as POC) is misleading since these are not pure POC sources. At the applied sonication power and in the absence of density fractionation, CN ratio assessments or isotopic ratios or mineralization assessments it is unclear what the ecological meaning of these fractions are, nor in how far the fractions really represent POC or rather more stable microaggregates and the C locked inside them (which the authors discuss also a bit). Thus, the interpretation of the data created by this fractionation scheme should be revised. I do find it interesting however to see clear distinctions between the fractions in terms of their qualitative properties that were derived with the MIR, which is a strong indication that “something different” has been isolated here, even though the exact meaning of this for C turnover is unclear. But this is certainly something worth exploring in a revised version.
- In general, I find it a bit difficult that there is so much inferences made from the spectra on both organic and inorganic soil components while no alternative assessment methods for organic or mineral features is provided. I am not saying that I do not trust the MIR data and the interpretation of it (the group is one of the leading groups worldwide in this field). But given the fact that (i) no real quantification of the identified groups of organic molecules or minerals present in the different fractions is made, (ii) that three very different soil samples are compared to each other and (iii) some interpretation of possible causal links between the different organic and mineral elements are made it remains speculative what the actually importance of the postulated stabilization mechanisms may be. This could be fixed by cross-checking the data with XRD spectroscopy, or simply calculating some element ratios (Al/Si, for example) for the cases of the mineralogy. For the organic phases I would recommend similar measures when it comes to interpreting C quality and stability.
- The applied dry combustion technique seems to cut-off the organic C phases after heating at 400°C and then 900°C for inorganic phases. There are many forms of organo-mineral associations that do remain stable at 400°C, and so some verification would need to be provided that those forms are net present here. The inorganic phase could also be assessed by other methods, if acidification of the samples prior to heating at higher temperatures than 400°C is not an option .
- The whole topic of potential interaction (in the introduction listed as a focus of this study) seems to be covered by Figure 7 and the correlations it presents. Not to speak that correlations are always problematic for deriving causality, but I am also lost in what I am supposed to learn from this figure. The caption also does not match the axis labels and it is unclear how I can see the three different soils in there. So for me, the topic of interactions between organic and mineral phases is not really covered in this manuscript in a satisfying way.
- Similar, the discussion does seem to rely a lot on correlative interpretations of the data, but it is not well linked to the different panels and tables that are presented in the manuscript. For me it was hard to follow the reasoning in there. To follow some of these arguments, we would need at least some sort of table or figure that shows the quantities of the different mineral and organic phases that are compared and linked here.
- In general, I think the discussion needs to flash out and make a very strong case for the novelty provided by this study, since many of the relationships that are described are well known for many years. Also some of the claims (for example that the spectra can be used to infer stability, line 236) need to be much better substantiated with actual experimental data on those soils or similar soils. Thus I think that also the conclusions that MIR can in C stabilization with minerals is not well supported.
Other comments:
- Not much is explained in terms of rationale behind the three selected soil types. Yes, they are on the lower end of SOC and have varying texture, but what are the other factors that explain those? Are they all equally weathered? From same or different climate zones? Same or different land use or geological background? Same soil depth? Same soil types? These things matter in order to understand the absence or presence of organic and mineral features, and also how C is stabilized.
- Recent literature has shown quite clearly that C stabilization depends quite clearly on reactive metal phases in soils, while the clay content across soil types (and clay types) is often not very helpful to understand its role in C stabilization. Have you thought about this here? I could not find something on this issue in the discussion or the data description.
- Given the size and prominence of figures 4-6 I find them a bit underused. In particular the panels from which not all are cited. I think more focus here on what you want to highlight (and why) might be helpful for the readers. You could use additional graphical amendments for example to illustrate the figures in a better way (just as you did for figure 2, which I found very helpful)
- You may want to revise Table 4 – what does it help you to list all these positions? Wouldn’t it make more sense here to provide a more condensed version that does provide some context in terms of what the (ecological or biogeochemical) importance of those assigned features may be? Like it is currently, it is just an overview table which information I forget as soon as I stop looking at it.
Minor comments:
- Two of the soil types are abbreviated (SL and SCL) while the third one is called Sandy soil or sometimes Sand (in tables). I find this confusing please revise.
- Table 1 and Table 3 in parts duplicate data for TOC. However, for the sandy soil the TOC value is different between both tables. Please explain.
Citation: https://doi.org/10.5194/egusphere-2023-2464-RC1 -
AC1: 'Reply on RC1', Lewis Walden, 23 Jan 2024
Publisher’s note: the supplement to this comment was edited on 23 January 2024. The adjustments were minor without effect on the scientific meaning.
We thank the reviewer for their comments on our manuscript. In the attached we provided our responses and outline changes to be made to the manuscript.
-
RC2: 'Comment on egusphere-2023-2464', Anonymous Referee #2, 20 Dec 2023
In their manuscript „Spectroscopic assessment of three ecologically distinct organic carbon fractions of mineral soils“ the authors present how MIR spectra can be used to identify organic matter composition and mineral components in two particle size fractions. This is surely an interesting and important aspect of using MIR spectra qualitative analysis of soils and can help to better understand carbon stabilisation in soils. However, the current manuscript does not clearly present a way forward to advance our understanding here. This is mainly caused by the more descriptive presentation of the results rather than an improvement and discussion of our mechanistic understanding. This is also related to the rather small set of soils and important missing information. Please see below my concerns and further comments.
Major concerns:
I struggle with the title and the use of the term “ecologically distinct”. While this sounds catchy, the authors do not discuss any ecological aspects of the two isolated fraction. To my opinion, the presented study does not include any data to discuss such ecological aspects. In consequence, the discussion section is rather a repetition of the results and the arguments that the presented findings are advancing our understanding are not well supported
The research aim to perform particle size fractionation of three different soils is rather weak and the novelty is not clear here. The second research aim is also more or less weak considering the small set of soils in this study. The general novelty is missing here.
One of my major issues is the presentation of the considered soils. It is not clear from section 2.1 from where the soils are, if they are derived from different climate, what soil types the represent, under which land use they were or from which depth. With all this basic information missing, it is not clear how relevant the presented findings are. I agree that there is a strong range of TOC and clay content, which will certainly affect the organic composition in the fractions. However, I would argue that a larger range would be need to include different stabilisation mechanisms. This would include a larger range of pH especially in the sandy soil to include changes in stabilisation processes by pedogenic oxides. The rational of only considering samples with TOC <2% is also not fully clear to me. The argument that we can use NMR for higher TOC soils is not convincing for me.
The authors present briefly why they selected a simple particle size fractionation. However, I would argue that for the intended purpose in this study, it is important to discuss the fact that the separation by size only can result in artifacts as a limitation. This is especially true when a large range of texture is considered. Thus, the POM of the sandy soils will be more diluted by sand than the POM in a clay rich soil, which might contain more stable aggregates. The logical consequences of this for the MIR analyses of the fraction is also presented in Line 167-174 and further discussed in the discussion. But as this is expected, it is not clear why the authors make this to the main part of the discussion. The authors do not provide any further discussion or any prove of what they actually separated by using other proxies such as d13C or C/N of the fractions determine plant derived or decomposed organic matter in the different fractions. This is especially critical considering the authors intention to study “ecologically relevant” pools.
Further comments:
The introduction gives a quite broad overview of several fractionation methods. However, some this seems rather to extensive and also some aspects are not fully correct. For example
Line 37-38: Doe the authors refer here to TG-DSC? This is not clear. The Cited paper is using Py-GC/MS which is more or less an evolving gas method and not a DSC. As far as I know, the thermal energy was modelled in the study by Sanderman and Grandy (2020). Please check this and also consider that there are more thermal methods
Line 39: Physical fractionation can involve both, particle and density separation and in combination.
Further, the whole setting and rational of this study is not clear from the introduction.
Line 57-59: This is stated because the study is performed on Australian soils? This is not clear from the introduction nor from the material and methods.
Table 1 it is not clear how the pH, TN and clay were measured
Table 2 and 4 seem to be repetitive.
Table 2 and 3 partly present the same parameters but different values for the TOC of the sand. Please clarify and avoid repetition. The fraction presentation of organic C (%) is also misleading here for the fractions. This is the actual TOC that is in each fraction rather than the fraction organic C, if I understand correctly. Please clarify this and also consider to present the relative share of each fraction on TOC.
Line 90-95: Do I understand correctly that the authors consider the TOC400 value as the total C? This would result in a large underestimation of organic carbon as a significant fraction is more stable than a combustion at 400°C. This is not a full combustion but only one defined thermal fraction.
Line 95: why does the TOC and TIC measurements result in distinct C fractions. Please revise this.
Line 104-105: What calibration do the authors mean here? I assume this corresponds to the background correction. Further, I assume that the authors performed a correction for H2O and CO2 interference. Please clarify.
Line 110-113: It is not clear to me why the authors performed a baseline correction and then SNV and SG correction. It is normally performed the other way around with baseline correction as the last step. What is the rational here? Also, did the authors perform a re-sampling prior to the SNC and SG?
Line 113-114: It is not clear what are the 27 observations when the replicate spectra were average and why is it only 425 wavenumbers?
Line 136-138: “To gain a better understanding of the features of the C fraction in relation to the whole soil, we multiplied the absorption values at each wavenumber by the proportion of each fraction in the whole soil.” Is not clear to me and I am not convinced that it is a correct step to divide the absorbance by a quantitative fraction proportion. Please explain the rational here.
Figure 2: I like the presentation in general. However, it is misleading that the different soils are presented and at the same time the general absorbance bands are explained. The bands for minerals, organics and the assignments are true for all soils because they are true for MIR spectra in general.
The Table 3 and Figure 2 are rather general description of the soils. Especially, figure 2 presents rather the expected spectra for the three different soils
Section 3.3 and Figure 7. I cannot fully follow the approach here and why the shown correlations would present a mechanism of stabilization. It would also be beneficial to separate here into the soils and fractions in the visualization. Especially for Fig. 7 b it is not clear if these three clusters are the soils of fractions. Please clarify the general use of this correlation.
Citation: https://doi.org/10.5194/egusphere-2023-2464-RC2 -
AC2: 'Reply on RC2', Lewis Walden, 23 Jan 2024
Publisher’s note: the supplement to this comment was edited on 23 January 2024. The adjustments were minor without effect on the scientific meaning.
We thank the reviewer for their comments on our manuscript. In the attached we provided our responses and outline changes to be made
-
AC2: 'Reply on RC2', Lewis Walden, 23 Jan 2024
Status: closed
-
RC1: 'Comment on egusphere-2023-2464', Anonymous Referee #1, 19 Dec 2023
Review for manuscript egusphere-2023-2464 for the journal Soil by Walden et al.
The manuscript describes the results of an MIR based spectroscopic analyses of three size-based soil organic matter fractions in low C-soils of Australia of varying texture and to test whether MIR spectra can discriminate between mineral and organic functional groups and explore relationships between them.
With this focus, the manuscript deals with an important topic that is worth exploring and could certainly provide insights that would help to close data gaps across soil types with respect to carbon storage, stabilization mechanisms and (potentially) carbon turnover. I do think however that the manuscript falls short at several occasions to provide what is to be expected from these objectives and the finally delivered novelty of the analyses is unclear to me.
My main concerns:
- The title speaks of “ecologically distinct” organic carbon fractions, but it remains unclear what this means for the authors. The applied fractionation scheme isolates size classes and not functional pools or fractions. In fact, the terms used in the manuscript (labeling the fractions >50µm as POC) is misleading since these are not pure POC sources. At the applied sonication power and in the absence of density fractionation, CN ratio assessments or isotopic ratios or mineralization assessments it is unclear what the ecological meaning of these fractions are, nor in how far the fractions really represent POC or rather more stable microaggregates and the C locked inside them (which the authors discuss also a bit). Thus, the interpretation of the data created by this fractionation scheme should be revised. I do find it interesting however to see clear distinctions between the fractions in terms of their qualitative properties that were derived with the MIR, which is a strong indication that “something different” has been isolated here, even though the exact meaning of this for C turnover is unclear. But this is certainly something worth exploring in a revised version.
- In general, I find it a bit difficult that there is so much inferences made from the spectra on both organic and inorganic soil components while no alternative assessment methods for organic or mineral features is provided. I am not saying that I do not trust the MIR data and the interpretation of it (the group is one of the leading groups worldwide in this field). But given the fact that (i) no real quantification of the identified groups of organic molecules or minerals present in the different fractions is made, (ii) that three very different soil samples are compared to each other and (iii) some interpretation of possible causal links between the different organic and mineral elements are made it remains speculative what the actually importance of the postulated stabilization mechanisms may be. This could be fixed by cross-checking the data with XRD spectroscopy, or simply calculating some element ratios (Al/Si, for example) for the cases of the mineralogy. For the organic phases I would recommend similar measures when it comes to interpreting C quality and stability.
- The applied dry combustion technique seems to cut-off the organic C phases after heating at 400°C and then 900°C for inorganic phases. There are many forms of organo-mineral associations that do remain stable at 400°C, and so some verification would need to be provided that those forms are net present here. The inorganic phase could also be assessed by other methods, if acidification of the samples prior to heating at higher temperatures than 400°C is not an option .
- The whole topic of potential interaction (in the introduction listed as a focus of this study) seems to be covered by Figure 7 and the correlations it presents. Not to speak that correlations are always problematic for deriving causality, but I am also lost in what I am supposed to learn from this figure. The caption also does not match the axis labels and it is unclear how I can see the three different soils in there. So for me, the topic of interactions between organic and mineral phases is not really covered in this manuscript in a satisfying way.
- Similar, the discussion does seem to rely a lot on correlative interpretations of the data, but it is not well linked to the different panels and tables that are presented in the manuscript. For me it was hard to follow the reasoning in there. To follow some of these arguments, we would need at least some sort of table or figure that shows the quantities of the different mineral and organic phases that are compared and linked here.
- In general, I think the discussion needs to flash out and make a very strong case for the novelty provided by this study, since many of the relationships that are described are well known for many years. Also some of the claims (for example that the spectra can be used to infer stability, line 236) need to be much better substantiated with actual experimental data on those soils or similar soils. Thus I think that also the conclusions that MIR can in C stabilization with minerals is not well supported.
Other comments:
- Not much is explained in terms of rationale behind the three selected soil types. Yes, they are on the lower end of SOC and have varying texture, but what are the other factors that explain those? Are they all equally weathered? From same or different climate zones? Same or different land use or geological background? Same soil depth? Same soil types? These things matter in order to understand the absence or presence of organic and mineral features, and also how C is stabilized.
- Recent literature has shown quite clearly that C stabilization depends quite clearly on reactive metal phases in soils, while the clay content across soil types (and clay types) is often not very helpful to understand its role in C stabilization. Have you thought about this here? I could not find something on this issue in the discussion or the data description.
- Given the size and prominence of figures 4-6 I find them a bit underused. In particular the panels from which not all are cited. I think more focus here on what you want to highlight (and why) might be helpful for the readers. You could use additional graphical amendments for example to illustrate the figures in a better way (just as you did for figure 2, which I found very helpful)
- You may want to revise Table 4 – what does it help you to list all these positions? Wouldn’t it make more sense here to provide a more condensed version that does provide some context in terms of what the (ecological or biogeochemical) importance of those assigned features may be? Like it is currently, it is just an overview table which information I forget as soon as I stop looking at it.
Minor comments:
- Two of the soil types are abbreviated (SL and SCL) while the third one is called Sandy soil or sometimes Sand (in tables). I find this confusing please revise.
- Table 1 and Table 3 in parts duplicate data for TOC. However, for the sandy soil the TOC value is different between both tables. Please explain.
Citation: https://doi.org/10.5194/egusphere-2023-2464-RC1 -
AC1: 'Reply on RC1', Lewis Walden, 23 Jan 2024
Publisher’s note: the supplement to this comment was edited on 23 January 2024. The adjustments were minor without effect on the scientific meaning.
We thank the reviewer for their comments on our manuscript. In the attached we provided our responses and outline changes to be made to the manuscript.
-
RC2: 'Comment on egusphere-2023-2464', Anonymous Referee #2, 20 Dec 2023
In their manuscript „Spectroscopic assessment of three ecologically distinct organic carbon fractions of mineral soils“ the authors present how MIR spectra can be used to identify organic matter composition and mineral components in two particle size fractions. This is surely an interesting and important aspect of using MIR spectra qualitative analysis of soils and can help to better understand carbon stabilisation in soils. However, the current manuscript does not clearly present a way forward to advance our understanding here. This is mainly caused by the more descriptive presentation of the results rather than an improvement and discussion of our mechanistic understanding. This is also related to the rather small set of soils and important missing information. Please see below my concerns and further comments.
Major concerns:
I struggle with the title and the use of the term “ecologically distinct”. While this sounds catchy, the authors do not discuss any ecological aspects of the two isolated fraction. To my opinion, the presented study does not include any data to discuss such ecological aspects. In consequence, the discussion section is rather a repetition of the results and the arguments that the presented findings are advancing our understanding are not well supported
The research aim to perform particle size fractionation of three different soils is rather weak and the novelty is not clear here. The second research aim is also more or less weak considering the small set of soils in this study. The general novelty is missing here.
One of my major issues is the presentation of the considered soils. It is not clear from section 2.1 from where the soils are, if they are derived from different climate, what soil types the represent, under which land use they were or from which depth. With all this basic information missing, it is not clear how relevant the presented findings are. I agree that there is a strong range of TOC and clay content, which will certainly affect the organic composition in the fractions. However, I would argue that a larger range would be need to include different stabilisation mechanisms. This would include a larger range of pH especially in the sandy soil to include changes in stabilisation processes by pedogenic oxides. The rational of only considering samples with TOC <2% is also not fully clear to me. The argument that we can use NMR for higher TOC soils is not convincing for me.
The authors present briefly why they selected a simple particle size fractionation. However, I would argue that for the intended purpose in this study, it is important to discuss the fact that the separation by size only can result in artifacts as a limitation. This is especially true when a large range of texture is considered. Thus, the POM of the sandy soils will be more diluted by sand than the POM in a clay rich soil, which might contain more stable aggregates. The logical consequences of this for the MIR analyses of the fraction is also presented in Line 167-174 and further discussed in the discussion. But as this is expected, it is not clear why the authors make this to the main part of the discussion. The authors do not provide any further discussion or any prove of what they actually separated by using other proxies such as d13C or C/N of the fractions determine plant derived or decomposed organic matter in the different fractions. This is especially critical considering the authors intention to study “ecologically relevant” pools.
Further comments:
The introduction gives a quite broad overview of several fractionation methods. However, some this seems rather to extensive and also some aspects are not fully correct. For example
Line 37-38: Doe the authors refer here to TG-DSC? This is not clear. The Cited paper is using Py-GC/MS which is more or less an evolving gas method and not a DSC. As far as I know, the thermal energy was modelled in the study by Sanderman and Grandy (2020). Please check this and also consider that there are more thermal methods
Line 39: Physical fractionation can involve both, particle and density separation and in combination.
Further, the whole setting and rational of this study is not clear from the introduction.
Line 57-59: This is stated because the study is performed on Australian soils? This is not clear from the introduction nor from the material and methods.
Table 1 it is not clear how the pH, TN and clay were measured
Table 2 and 4 seem to be repetitive.
Table 2 and 3 partly present the same parameters but different values for the TOC of the sand. Please clarify and avoid repetition. The fraction presentation of organic C (%) is also misleading here for the fractions. This is the actual TOC that is in each fraction rather than the fraction organic C, if I understand correctly. Please clarify this and also consider to present the relative share of each fraction on TOC.
Line 90-95: Do I understand correctly that the authors consider the TOC400 value as the total C? This would result in a large underestimation of organic carbon as a significant fraction is more stable than a combustion at 400°C. This is not a full combustion but only one defined thermal fraction.
Line 95: why does the TOC and TIC measurements result in distinct C fractions. Please revise this.
Line 104-105: What calibration do the authors mean here? I assume this corresponds to the background correction. Further, I assume that the authors performed a correction for H2O and CO2 interference. Please clarify.
Line 110-113: It is not clear to me why the authors performed a baseline correction and then SNV and SG correction. It is normally performed the other way around with baseline correction as the last step. What is the rational here? Also, did the authors perform a re-sampling prior to the SNC and SG?
Line 113-114: It is not clear what are the 27 observations when the replicate spectra were average and why is it only 425 wavenumbers?
Line 136-138: “To gain a better understanding of the features of the C fraction in relation to the whole soil, we multiplied the absorption values at each wavenumber by the proportion of each fraction in the whole soil.” Is not clear to me and I am not convinced that it is a correct step to divide the absorbance by a quantitative fraction proportion. Please explain the rational here.
Figure 2: I like the presentation in general. However, it is misleading that the different soils are presented and at the same time the general absorbance bands are explained. The bands for minerals, organics and the assignments are true for all soils because they are true for MIR spectra in general.
The Table 3 and Figure 2 are rather general description of the soils. Especially, figure 2 presents rather the expected spectra for the three different soils
Section 3.3 and Figure 7. I cannot fully follow the approach here and why the shown correlations would present a mechanism of stabilization. It would also be beneficial to separate here into the soils and fractions in the visualization. Especially for Fig. 7 b it is not clear if these three clusters are the soils of fractions. Please clarify the general use of this correlation.
Citation: https://doi.org/10.5194/egusphere-2023-2464-RC2 -
AC2: 'Reply on RC2', Lewis Walden, 23 Jan 2024
Publisher’s note: the supplement to this comment was edited on 23 January 2024. The adjustments were minor without effect on the scientific meaning.
We thank the reviewer for their comments on our manuscript. In the attached we provided our responses and outline changes to be made
-
AC2: 'Reply on RC2', Lewis Walden, 23 Jan 2024
Viewed
| HTML | XML | Total | Supplement | BibTeX | EndNote | |
|---|---|---|---|---|---|---|
| 211 | 57 | 19 | 287 | 24 | 10 | 11 |
- HTML: 211
- PDF: 57
- XML: 19
- Total: 287
- Supplement: 24
- BibTeX: 10
- EndNote: 11
Viewed (geographical distribution)
| Country | # | Views | % |
|---|
| Total: | 0 |
| HTML: | 0 |
| PDF: | 0 |
| XML: | 0 |
- 1