the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 10 Mar 2022
Large-diameter trees control forest structure and function in successional temperate forests
Abstract. Large-diameter trees regulate forest diversity, structure and aboveground biomass (AGB), but the mechanisms whereby they control forest processes remain understudied, especially in early successional forests. We used 1,956 0.16 ha plots from the Korean National Forest Inventory from mostly 20–50 years old stands (biomass accumulation phase) in closed-canopy temperate forests, with 236 species of woody plants and 391,543 individual stems ≥ 6 cm diameter at breast height. Based hereon, we analyzed the effects of large-diameter trees on aboveground biomass (AGB) in the overstory, understory, and the two combined (total vegetation). We also considered the effects of species and functional diversity, functional dominance of traits, stem density, and abiotic drivers (i.e., topographic, climatic and edaphic variables) interacting with large-diameter trees on AGB. We performed model averaging approaches with backward stepwise regressions and piecewise structural equation modeling to quantify and compare the effects of large trees vs. other biotic and abiotic drivers. Overall, large-diameter trees had a dominant effect on AGB compared with remaining tree attributes and abiotic drivers for both the overstory and whole community; however, they did not strongly influence the understory. Large-diameter trees also modulated the strength of the direct effects of abiotic drivers, particularly soil fertility, on AGB, as well as indirect effects via regulating the attributes of smaller-diameter trees. Our study provides new insights into the mechanisms associated with self-thinning and resource availability whereby large-diameter trees drive high AGB in succession forests. We also show that the effect of large-diameter trees is forest stratum-dependent across different types of temperate forests. This study emphasizes the importance of large-diameter trees in determining the structure and function in early successional forests, and the need for conservation and management actions to protect and promote these keystone organisms.
This preprint has been withdrawn.
-
Withdrawal notice
This preprint has been withdrawn.
-
Preprint
(1097 KB)
-
Supplement
(2229 KB)
-
This preprint has been withdrawn.
- Preprint
(1097 KB) - Metadata XML
-
Supplement
(2229 KB) - BibTeX
- EndNote
Interactive discussion
Status: closed
-
RC1: 'Comment on bg-2022-60', Anonymous Referee #1, 30 Apr 2022
Review for BG: Large-diameter trees control forest structure and function in successional temperate forests, from Chang-Bae Lee et al.
General comments
I congratulate the authors for the manuscript, which shows the importance of large-sized trees for the biomass storage across temperate successional forests. The manuscript is very well written, the text is fluid and very well supported. In my estimation, the authors did well in the data analysis, but maybe too much for one manuscript; therefore, my main suggestion is to evaluate the needs of the two approaches to understand the effect of the chosen predictors on AGB. I hope that my suggestions contribute to the manuscript improvement. Best regards.
Specific comments
L34: I don’t think that “phenomenon” is the best word to describe it here. Maybe condition suits better?
L59: To be acquisitive or conservative depends largely on the forest moisture, i.e., wet or dry forest (see Poorter et al 2019 Nature, doi.org/10.1038/s41559-019-0882-6). Thus, be cautious in making this assumption.
L77: “metric” is more likely to be related to a combination of variables, e.g. an index. In your case, the large-trees mean a variable.
L83: Why not in the understory?
L85: Does your study region have drought periods?
L87: This may not be totally true. Soil is certainly important, but light availability is as important as soil fertility.
L112: As I understood, the authors do have the information of tree dbh, but the AGB was estimated from the tree volume information. Why did you choose this approach? Did you perform any comparison from the biomass estimated via dbh or via tree volume? I am concerned about future comparisons. Most part of the AGB estimations from forests across the world are based on tree dbh, and this approach via volume may be not entirely comparable.
Table S2: The predictor’s values for 99% remaining trees and understory trees are quite similar, aren’t them? This makes me think if the classification adopted by the authors is the best to describe forest strata differences. Did you consider splitting the data by different size classes?
L154-L157: I am afraid that you cannot perform a PCA with those topographical data. According to Legendre and Legendre (cited), the correct procedure should be a PCoA, due to the nature of the data (non-continuous data, such as latitude and longitude). Please revise and correct.
L168-L187: The data analysis description is a bit confusing to understand. Consider showing this information in a table, it will be much easier to follow. Regarding the model selection, why did you perform a backward selection via stepAIC to select the best model, instead just a simple AIC? The backward model selection is used to test candidate models by removing variables, and if I understood, this was done again via dredge function. I suggest performing a simple AIC to compare the five candidate models, and then apply a dredge function the model with lowest AIC.
L188-L192: I did not understand why you performed multiple regressions as well as the pSEM model. In my estimation, those two analyses are too much for one manuscript, making the overall message confuse. Consider removing one of those approaches, focusing on the multiple regressions or the structural model, and not both. I suggest showing only the multiple regressions results.
L224-L226: I understand your point, but I recommend being cautious with this suggestion. To improve the carbon sequestration is good to remove more carbon from atmosphere, but by managing these forests and removing large trees, all their carbon will be released, and the balance from gains and losses (net carbon change) may become negative, which is not the intention.
Technical comments
L73: Did you mean “poorly known” instead of unknown?
L79: standing biomass?
L139-L141: You mention that four traits were selected to perform functional analysis; however, just three are described. At line 143 you mention three traits. Maybe the previous sentence is incorrect, please check it. Additionally, is there any particular reason for not using WD as a predictor?
L150: NFT or NFI?
L215: No needs to mention dbh here.
L242: Correct “severe”
L329: Correct “climatic”
Citation: https://doi.org/10.5194/bg-2022-60-RC1 -
CC1: 'Comment on bg-2022-60', Sylvanus Mensah, 04 Dec 2022
Chang-Bae Lee e al. produced a manuscript on Large-diameter trees and forest structure and function in successional temperate forests.
The authors made use of existing 1,956 0.16 ha plots from the Korean National Forest Inventory from mostly 20–50 years old stands (biomass accumulation phase) in closed canopy temperate forests, with 236 species of woody plants and 391,543 individual stems ≥ 6 cm diameter at breast height.
Overall, the authors found that large-diameter trees had a dominant effect on AGB compared with remaining tree attributes and abiotic drivers for both the overstory and whole community; but not in the understory. I have noted several issues and flaws in this paper, which should be reconsidered by its authors. Prominent ones are the similarity with previously published papers by the same team and lack of knowledge gap, sampling inappropriateness, and statistical/reporting mistakes. The current manuscript is not suitable for publication.
After reading the whole manuscript, I think there is a disconnect between the title and the subject of study here. I do not believe that a study of biomass (aboveground biomass) is sufficient for authors to generalize this to forest functions. Aboveground biomass alone is not enough to provide generality on ecosystem functions. Please revise the title to reflect what is being studied in this paper.
Second, I am not convinced that temperate forests in Korea are representative samples of temperate forests across the globe. So please again revise the title for more specificity.
I did not see any new insights from what we already know and that the same team of authors have previously published. Where is the knowledge gap here? Authors talked about forest succession, but did not even account for the successional stages in their analyses. On the contrary, the authors have just endorsed findings from most previous studies, and just to mention the initial papers by (Lutz et al. 2012; Lutz et al. 2013) and the few papers below:
Lutz et al. 2018. Global importance of large-diameter trees, Glob. Ecol. Biogeogr., 27, 849–864, https://doi.org/10.1111/geb.12747
Ali et al. 2019 Big-sized trees overrule remaining trees’ attributes and species richness as determinants of aboveground biomass in tropical forests, Glob. Chang. Biol., 25, 2810–2824
Ali, A., et al.2020 Big-tree–energy mechanism underlies forest diversity and aboveground biomass, For. Ecol. Manag., 462
Ali, A., and Wang, L. Q. 2021: Big-sized trees and forest functioning: current knowledge and future perspectives, 360 Ecol. Indic., 127
Yuan, Z., Ali, A., Sanaei, A., et al. 2021 : Few large trees, rather than plant diversity and composition, drive the above-ground biomass stock and dynamics of temperate forests in northeast China, For. Ecol. Manag., 481
I did not see much difference between these papers and the manuscript presented here. All of what is described in this manuscript have appeared in different forms in many of the above papers. It is hard to see the specific advance here. The authors need to do a much better job in presenting the novelty and the added value in this manuscript, else, I see this more like a replication or a “cookie cutter” of previous studies with no much scholarship on its own. This also applies to the arguments, and analytical methods presented in this manuscript. Linked to the latter, I point out my additional major concerns:
First. The study failed to be more analytical to avoid linear testing of the effects of “part of the sum”. Their definition of large-sized trees is based on the largest 1% tree in each plot. As such, there is no other alternative for large sized trees than to be the most determining factor here, because they represent the big part of the sum. Even in plot with lowest AGB, you will still have relatively bigger tree (see line 130, where you had the large-diameter threshold varying from 12 cm to 91.5 cm) that forms part of that plot biomass. So this means that in each plot you will see that large size trees contribute highly to AGB. So do we expect otherwise? It would make a bit of sense, if large-size trees were determined at community level (i.e. across all plot), then used to differentiate for each plot. Again, be careful of the metric being used because of the potential circularity and high collinearity.
Second. Authors said they used 1956 plots of 0.16ha (line 16). In lines 105-107, they made use of 4 plots of 0.04ha each. This means that the initial sampling unit was not 0.16ha, but 0.04ha. How can we really assess large-sized trees and forest structure in plots of 0.04 ha (20x20m), which are much convenient for herbs/phytosociology/releve survey. Although they have combined 4 plots of 0.04ha to make it 0.16ha, this remains a flaw because initial sampling units cannot just be aggregated to form analytical units, without proper accounting for hierarchical/nesting methods.
Third. The designation of understory here is also problematic. In line 106, they have only considered trees with dbh >6 cm, ignoring all plants in the < 6cm dbh classes. As such, it seems that the true contribution of the understorey is being ignored here. So how can we talk about understorey when trees in class of < 6 cm dbh are not considered. This is a methodological flaw that needs to be addressed in the analyses. It is further strange that authors did not consider wood density as a relevant trait here for biomass, but used seed mass???.
Four. From my last two comments, it is clear that the sampling design is not appropriate for this study, or at least for the research questions. As we all know, national forest inventories are primarily carried out for purposes other than assessing biodiversity-ecosystem function relationship and I am very critical of studies that use samplings that are not initially designed for a given study. In fact, in lines 101-102, authors state that the NFI protocol has been designed and implemented to monitor changes in forest resources and forest cover.
Five. Statistical analyses are not clear and problematic. Did the authors use generalized least squares models for all the response variables? Authors affirmed that was no evidence for spatial autocorrelation because AIC values for non-spatial models were lower than those for spatial models. This is a wrong way of testing spatial autocorrelation and the references (Yuan et al., 2019; Chun et al., 2020) provided are from the same team of authors and cannot be used to justify this. Please provide the Moran’s Index test statistic for each of the models. Looking at the environmental data, there is no information on the grid of the soil and climatic data collected. Obviously, we expect strong spatial components here looking at the smaller plot size. This reinforces the need for appropriate spatial autocorrelation test.
Six. Still in the statistical analyses sections, there is no need to transform predictors, what we are interested in is the distribution of the residuals of each model. Please provide this information along with the shapiro-wilk test to cross-check how normality and linearity were improved as you stated in line 164.
Further, with the variation of the age class of the plots, why was age not considered in the analyses? With age being left out, I do not think the analyses conducted here bring any reliable conclusion of ecological processes as described in the manuscript. Also, the whole section on the statistical analyses need to be revised to link to each hypothesis/research question. As it stands, it is very bulky and one could not know exactly which analyses are responding to which question/hypothesis.
Seven. The rationale for the piecewise SEM is not provided, and I am not sure if you can test the indirect effects with piecewiseSEM as you stated in line 189. If yes, please explain this. I know lavaan has a clinical way of doing this based on global estimation, but I think pSEM is more of local estimation with sub-set models. Again, authors need to present the results of these sub-set models (not as graphics as it is now in the appendix). What are the different sub-set models? This is even more critical since you have multiple response variables here, and we do not know if all of them were fitted with the same type of model. Please ensure that you report statistics appropriately, with respect to your questions, from the different models tested. Please provide R codes for us to counter check accuracy of these results.
Eight. Today, what we are interested in is a more biological link that explains the results. Yes SEM has been widely used in BEF studies, but it is not a pass code. They only provide "causal links" and we should go beyond significant SEM links. Trait-based modeling or experiment, but statistical analyses like these will not provide robust findings, rather showing the obvious!
Below are my specific comments
Abstract
Line 16: which forest processes are the authors referring to? Are those forest processes being studied here? If yes, please provide details
Line 17: 20 to 50 years age of stand provide considerable variance for you to consider the effect of age in the analyses. I suggest that effect of age be considered here
Lines 15- 20. Logic is missing here. First provide the background and gap of the study, then the objectives/hypotheses to address the gap, and after the method/sampling design used.
Line 20: Why did you consider the effects of functional diversity, functional dominance of traits, stem density, and abiotic drivers? You did not provide any background to this
Lines 23-25: Nothing new here
Line 27: self-thinning? Please moderate your stance
Lines 28-29: How can we be convinced about your conclusion on the effect of large trees across forest strata, when you only studied stem with > 6 cm dbh. Does this make sense?
Line 29-31: above ground biomass if far from telling us a complete story on ecosystem function. So please again avoid un-founded conclusions
Introduction
Line 35: what do you mean by the “mechanisms of biomass dominance”?
Line 37: “carbon sequestration is distributed”?? Please revise
Line 33-43: This first paragraph lacks logic in the succession of ideas: in the same paragraph, you introduced in this order, large-diameter trees, mechanisms of biomass dominance (which you did not explain), carbon sequestration in younger trees, forests potential for carbon stock. Please revise this to provide more logic as you introduce an idea at the beginning of your paragraph
Line 44 -48: You are not saying anything relevant here. At least, I expect that you provide state of art background on the contrasting effects of abiotic factors on AGB, rather than just citing them.
Line 48-50: for consistency, I expect that you give exemple of biotic factors, and how they affect AGB.
Line 50-51: Please revise this. Not well stated
Line 52: What about the selection effects? Please explain how the mass-ratio is linked to selection/sampling effect
Line 82-84: why not in the understory? Please expand futher
Line 84-86: The hypotheses are not specific here. Please provide expected direction of the effects. Is aridity not derived from other climatic factors?
Line 87: Which edaphic factor? And how?
Material and Methods
Line 105: Actually, authors combined 4 subplots of 0.04ha to make the 0.16ha. How confidently can we assess large size trees in 0.04 ha subplot. The observation unit is too small for this kind of study.
Line 115-116: It is no acceptable to talk about understory when you have only considered tees with dbh>6cm
Citation: https://doi.org/10.5194/bg-2022-60-CC1 -
RC2: 'Comment on bg-2022-60', Anonymous Referee #2, 08 Dec 2022
Chang-Bae Lee e al. produced a manuscript on Large-diameter trees and forest structure and function in successional temperate forests.
The authors made use of existing 1,956 0.16 ha plots from the Korean National Forest Inventory from mostly 20–50 years old stands (biomass accumulation phase) in closed canopy temperate forests, with 236 species of woody plants and 391,543 individual stems ≥ 6 cm diameter at breast height.
Overall, the authors found that large-diameter trees had a dominant effect on AGB compared with remaining tree attributes and abiotic drivers for both the overstory and whole community; but not in the understory. I have noted several issues and flaws in this paper, which should be reconsidered by its authors. Prominent ones are the similarity with previously published papers by the same team and lack of knowledge gap, sampling inappropriateness, and statistical/reporting mistakes. The current manuscript is not suitable for publication.
After reading the whole manuscript, I think there is a disconnect between the title and the subject of study here. I do not believe that a study of biomass (aboveground biomass) is sufficient for authors to generalize this to forest functions. Aboveground biomass alone is not enough to provide generality on ecosystem functions. Please revise the title to reflect what is being studied in this paper.
Second, I am not convinced that temperate forests in Korea are representative samples of temperate forests across the globe. So please again revise the title for more specificity.
I did not see any new insights from what we already know and that the same team of authors have previously published. Where is the knowledge gap here? Authors talked about forest succession, but did not even account for the successional stages in their analyses. On the contrary, the authors have just endorsed findings from most previous studies, and just to mention the initial papers by (Lutz et al. 2012; Lutz et al. 2013) and the few papers below:
Lutz et al. 2018. Global importance of large-diameter trees, Glob. Ecol. Biogeogr., 27, 849–864, https://doi.org/10.1111/geb.12747
Ali et al. 2019 Big-sized trees overrule remaining trees’ attributes and species richness as determinants of aboveground biomass in tropical forests, Glob. Chang. Biol., 25, 2810–2824
Ali, A., et al.2020 Big-tree–energy mechanism underlies forest diversity and aboveground biomass, For. Ecol. Manag., 462
Ali, A., and Wang, L. Q. 2021: Big-sized trees and forest functioning: current knowledge and future perspectives, 360 Ecol. Indic., 127
Yuan, Z., Ali, A., Sanaei, A., et al. 2021 : Few large trees, rather than plant diversity and composition, drive the above-ground biomass stock and dynamics of temperate forests in northeast China, For. Ecol. Manag., 481
I did not see much difference between these papers and the manuscript presented here. All of what is described in this manuscript have appeared in different forms in many of the above papers. It is hard to see the specific advance here. The authors need to do a much better job in presenting the novelty and the added value in this manuscript, else, I see this more like a replication or a “cookie cutter” of previous studies with no much scholarship on its own. This also applies to the arguments, and analytical methods presented in this manuscript. Linked to the latter, I point out my additional major concerns:
First. The study failed to be more analytical to avoid linear testing of the effects of “part of the sum”. Their definition of large-sized trees is based on the largest 1% tree in each plot. As such, there is no other alternative for large sized trees than to be the most determining factor here, because they represent the big part of the sum. Even in plot with lowest AGB, you will still have relatively bigger tree (see line 130, where you had the large-diameter threshold varying from 12 cm to 91.5 cm) that forms part of that plot biomass. So this means that in each plot you will see that large size trees contribute highly to AGB. So do we expect otherwise? It would make a bit of sense, if large-size trees were determined at community level (i.e. across all plot), then used to differentiate for each plot. Again, be careful of the metric being used because of the potential circularity and high collinearity.
Second. Authors said they used 1956 plots of 0.16ha (line 16). In lines 105-107, they made use of 4 plots of 0.04ha each. This means that the initial sampling unit was not 0.16ha, but 0.04ha. How can we really assess large-sized trees and forest structure in plots of 0.04 ha (20x20m), which are much convenient for herbs/phytosociology/releve survey. Although they have combined 4 plots of 0.04ha to make it 0.16ha, this remains a flaw because initial sampling units cannot just be aggregated to form analytical units, without proper accounting for hierarchical/nesting methods.
Third. The designation of understory here is also problematic. In line 106, they have only considered trees with dbh >6 cm, ignoring all plants in the < 6cm dbh classes. As such, it seems that the true contribution of the understorey is being ignored here. So how can we talk about understorey when trees in class of < 6 cm dbh are not considered. This is a methodological flaw that needs to be addressed in the analyses. It is further strange that authors did not consider wood density as a relevant trait here for biomass, but used seed mass???.
Four. From my last two comments, it is clear that the sampling design is not appropriate for this study, or at least for the research questions. As we all know, national forest inventories are primarily carried out for purposes other than assessing biodiversity-ecosystem function relationship and I am very critical of studies that use samplings that are not initially designed for a given study. In fact, in lines 101-102, authors state that the NFI protocol has been designed and implemented to monitor changes in forest resources and forest cover.
Five. Statistical analyses are not clear and problematic. Did the authors use generalized least squares models for all the response variables? Authors affirmed that was no evidence for spatial autocorrelation because AIC values for non-spatial models were lower than those for spatial models. This is a wrong way of testing spatial autocorrelation and the references (Yuan et al., 2019; Chun et al., 2020) provided are from the same team of authors and cannot be used to justify this. Please provide the Moran’s Index test statistic for each of the models. Looking at the environmental data, there is no information on the grid of the soil and climatic data collected. Obviously, we expect strong spatial components here looking at the smaller plot size. This reinforces the need for appropriate spatial autocorrelation test.
Six. Still in the statistical analyses sections, there is no need to transform predictors, what we are interested in is the distribution of the residuals of each model. Please provide this information along with the shapiro-wilk test to cross-check how normality and linearity were improved as you stated in line 164.
Further, with the variation of the age class of the plots, why was age not considered in the analyses? With age being left out, I do not think the analyses conducted here bring any reliable conclusion of ecological processes as described in the manuscript. Also, the whole section on the statistical analyses need to be revised to link to each hypothesis/research question. As it stands, it is very bulky and one could not know exactly which analyses are responding to which question/hypothesis.
Seven. The rationale for the piecewise SEM is not provided, and I am not sure if you can test the indirect effects with piecewiseSEM as you stated in line 189. If yes, please explain this. I know lavaan has a clinical way of doing this based on global estimation, but I think pSEM is more of local estimation with sub-set models. Again, authors need to present the results of these sub-set models (not as graphics as it is now in the appendix). What are the different sub-set models? This is even more critical since you have multiple response variables here, and we do not know if all of them were fitted with the same type of model. Please ensure that you report statistics appropriately, with respect to your questions, from the different models tested. Please provide R codes for us to counter check accuracy of these results.
Eight. Today, what we are interested in is a more biological link that explains the results. Yes SEM has been widely used in BEF studies, but it is not a pass code. They only provide "causal links" and we should go beyond significant SEM links. Trait-based modeling or experiment, but statistical analyses like these will not provide robust findings, rather showing the obvious!
Below are my specific comments
Abstract
Line 16: which forest processes are the authors referring to? Are those forest processes being studied here? If yes, please provide details
Line 17: 20 to 50 years age of stand provide considerable variance for you to consider the effect of age in the analyses. I suggest that effect of age be considered here
Lines 15- 20. Logic is missing here. First provide the background and gap of the study, then the objectives/hypotheses to address the gap, and after the method/sampling design used.
Line 20: Why did you consider the effects of functional diversity, functional dominance of traits, stem density, and abiotic drivers? You did not provide any background to this
Lines 23-25: Nothing new here
Line 27: self-thinning? Please moderate your stance
Lines 28-29: How can we be convinced about your conclusion on the effect of large trees across forest strata, when you only studied stem with > 6 cm dbh. Does this make sense?
Line 29-31: above ground biomass if far from telling us a complete story on ecosystem function. So please again avoid un-founded conclusions
Introduction
Line 35: what do you mean by the “mechanisms of biomass dominance”?
Line 37: “carbon sequestration is distributed”?? Please revise
Line 33-43: This first paragraph lacks logic in the succession of ideas: in the same paragraph, you introduced in this order, large-diameter trees, mechanisms of biomass dominance (which you did not explain), carbon sequestration in younger trees, forests potential for carbon stock. Please revise this to provide more logic as you introduce an idea at the beginning of your paragraph
Line 44 -48: You are not saying anything relevant here. At least, I expect that you provide state of art background on the contrasting effects of abiotic factors on AGB, rather than just citing them.
Line 48-50: for consistency, I expect that you give exemple of biotic factors, and how they affect AGB.
Line 50-51: Please revise this. Not well stated
Line 52: What about the selection effects? Please explain how the mass-ratio is linked to selection/sampling effect
Line 82-84: why not in the understory? Please expand futher
Line 84-86: The hypotheses are not specific here. Please provide expected direction of the effects. Is aridity not derived from other climatic factors?
Line 87: Which edaphic factor? And how?
Material and Methods
Line 105: Actually, authors combined 4 subplots of 0.04ha to make the 0.16ha. How confidently can we assess large size trees in 0.04 ha subplot. The observation unit is too small for this kind of study.
Line 115-116: It is no acceptable to talk about understory when you have only considered tees with dbh>6cm
Citation: https://doi.org/10.5194/bg-2022-60-RC2
Interactive discussion
Status: closed
-
RC1: 'Comment on bg-2022-60', Anonymous Referee #1, 30 Apr 2022
Review for BG: Large-diameter trees control forest structure and function in successional temperate forests, from Chang-Bae Lee et al.
General comments
I congratulate the authors for the manuscript, which shows the importance of large-sized trees for the biomass storage across temperate successional forests. The manuscript is very well written, the text is fluid and very well supported. In my estimation, the authors did well in the data analysis, but maybe too much for one manuscript; therefore, my main suggestion is to evaluate the needs of the two approaches to understand the effect of the chosen predictors on AGB. I hope that my suggestions contribute to the manuscript improvement. Best regards.
Specific comments
L34: I don’t think that “phenomenon” is the best word to describe it here. Maybe condition suits better?
L59: To be acquisitive or conservative depends largely on the forest moisture, i.e., wet or dry forest (see Poorter et al 2019 Nature, doi.org/10.1038/s41559-019-0882-6). Thus, be cautious in making this assumption.
L77: “metric” is more likely to be related to a combination of variables, e.g. an index. In your case, the large-trees mean a variable.
L83: Why not in the understory?
L85: Does your study region have drought periods?
L87: This may not be totally true. Soil is certainly important, but light availability is as important as soil fertility.
L112: As I understood, the authors do have the information of tree dbh, but the AGB was estimated from the tree volume information. Why did you choose this approach? Did you perform any comparison from the biomass estimated via dbh or via tree volume? I am concerned about future comparisons. Most part of the AGB estimations from forests across the world are based on tree dbh, and this approach via volume may be not entirely comparable.
Table S2: The predictor’s values for 99% remaining trees and understory trees are quite similar, aren’t them? This makes me think if the classification adopted by the authors is the best to describe forest strata differences. Did you consider splitting the data by different size classes?
L154-L157: I am afraid that you cannot perform a PCA with those topographical data. According to Legendre and Legendre (cited), the correct procedure should be a PCoA, due to the nature of the data (non-continuous data, such as latitude and longitude). Please revise and correct.
L168-L187: The data analysis description is a bit confusing to understand. Consider showing this information in a table, it will be much easier to follow. Regarding the model selection, why did you perform a backward selection via stepAIC to select the best model, instead just a simple AIC? The backward model selection is used to test candidate models by removing variables, and if I understood, this was done again via dredge function. I suggest performing a simple AIC to compare the five candidate models, and then apply a dredge function the model with lowest AIC.
L188-L192: I did not understand why you performed multiple regressions as well as the pSEM model. In my estimation, those two analyses are too much for one manuscript, making the overall message confuse. Consider removing one of those approaches, focusing on the multiple regressions or the structural model, and not both. I suggest showing only the multiple regressions results.
L224-L226: I understand your point, but I recommend being cautious with this suggestion. To improve the carbon sequestration is good to remove more carbon from atmosphere, but by managing these forests and removing large trees, all their carbon will be released, and the balance from gains and losses (net carbon change) may become negative, which is not the intention.
Technical comments
L73: Did you mean “poorly known” instead of unknown?
L79: standing biomass?
L139-L141: You mention that four traits were selected to perform functional analysis; however, just three are described. At line 143 you mention three traits. Maybe the previous sentence is incorrect, please check it. Additionally, is there any particular reason for not using WD as a predictor?
L150: NFT or NFI?
L215: No needs to mention dbh here.
L242: Correct “severe”
L329: Correct “climatic”
Citation: https://doi.org/10.5194/bg-2022-60-RC1 -
CC1: 'Comment on bg-2022-60', Sylvanus Mensah, 04 Dec 2022
Chang-Bae Lee e al. produced a manuscript on Large-diameter trees and forest structure and function in successional temperate forests.
The authors made use of existing 1,956 0.16 ha plots from the Korean National Forest Inventory from mostly 20–50 years old stands (biomass accumulation phase) in closed canopy temperate forests, with 236 species of woody plants and 391,543 individual stems ≥ 6 cm diameter at breast height.
Overall, the authors found that large-diameter trees had a dominant effect on AGB compared with remaining tree attributes and abiotic drivers for both the overstory and whole community; but not in the understory. I have noted several issues and flaws in this paper, which should be reconsidered by its authors. Prominent ones are the similarity with previously published papers by the same team and lack of knowledge gap, sampling inappropriateness, and statistical/reporting mistakes. The current manuscript is not suitable for publication.
After reading the whole manuscript, I think there is a disconnect between the title and the subject of study here. I do not believe that a study of biomass (aboveground biomass) is sufficient for authors to generalize this to forest functions. Aboveground biomass alone is not enough to provide generality on ecosystem functions. Please revise the title to reflect what is being studied in this paper.
Second, I am not convinced that temperate forests in Korea are representative samples of temperate forests across the globe. So please again revise the title for more specificity.
I did not see any new insights from what we already know and that the same team of authors have previously published. Where is the knowledge gap here? Authors talked about forest succession, but did not even account for the successional stages in their analyses. On the contrary, the authors have just endorsed findings from most previous studies, and just to mention the initial papers by (Lutz et al. 2012; Lutz et al. 2013) and the few papers below:
Lutz et al. 2018. Global importance of large-diameter trees, Glob. Ecol. Biogeogr., 27, 849–864, https://doi.org/10.1111/geb.12747
Ali et al. 2019 Big-sized trees overrule remaining trees’ attributes and species richness as determinants of aboveground biomass in tropical forests, Glob. Chang. Biol., 25, 2810–2824
Ali, A., et al.2020 Big-tree–energy mechanism underlies forest diversity and aboveground biomass, For. Ecol. Manag., 462
Ali, A., and Wang, L. Q. 2021: Big-sized trees and forest functioning: current knowledge and future perspectives, 360 Ecol. Indic., 127
Yuan, Z., Ali, A., Sanaei, A., et al. 2021 : Few large trees, rather than plant diversity and composition, drive the above-ground biomass stock and dynamics of temperate forests in northeast China, For. Ecol. Manag., 481
I did not see much difference between these papers and the manuscript presented here. All of what is described in this manuscript have appeared in different forms in many of the above papers. It is hard to see the specific advance here. The authors need to do a much better job in presenting the novelty and the added value in this manuscript, else, I see this more like a replication or a “cookie cutter” of previous studies with no much scholarship on its own. This also applies to the arguments, and analytical methods presented in this manuscript. Linked to the latter, I point out my additional major concerns:
First. The study failed to be more analytical to avoid linear testing of the effects of “part of the sum”. Their definition of large-sized trees is based on the largest 1% tree in each plot. As such, there is no other alternative for large sized trees than to be the most determining factor here, because they represent the big part of the sum. Even in plot with lowest AGB, you will still have relatively bigger tree (see line 130, where you had the large-diameter threshold varying from 12 cm to 91.5 cm) that forms part of that plot biomass. So this means that in each plot you will see that large size trees contribute highly to AGB. So do we expect otherwise? It would make a bit of sense, if large-size trees were determined at community level (i.e. across all plot), then used to differentiate for each plot. Again, be careful of the metric being used because of the potential circularity and high collinearity.
Second. Authors said they used 1956 plots of 0.16ha (line 16). In lines 105-107, they made use of 4 plots of 0.04ha each. This means that the initial sampling unit was not 0.16ha, but 0.04ha. How can we really assess large-sized trees and forest structure in plots of 0.04 ha (20x20m), which are much convenient for herbs/phytosociology/releve survey. Although they have combined 4 plots of 0.04ha to make it 0.16ha, this remains a flaw because initial sampling units cannot just be aggregated to form analytical units, without proper accounting for hierarchical/nesting methods.
Third. The designation of understory here is also problematic. In line 106, they have only considered trees with dbh >6 cm, ignoring all plants in the < 6cm dbh classes. As such, it seems that the true contribution of the understorey is being ignored here. So how can we talk about understorey when trees in class of < 6 cm dbh are not considered. This is a methodological flaw that needs to be addressed in the analyses. It is further strange that authors did not consider wood density as a relevant trait here for biomass, but used seed mass???.
Four. From my last two comments, it is clear that the sampling design is not appropriate for this study, or at least for the research questions. As we all know, national forest inventories are primarily carried out for purposes other than assessing biodiversity-ecosystem function relationship and I am very critical of studies that use samplings that are not initially designed for a given study. In fact, in lines 101-102, authors state that the NFI protocol has been designed and implemented to monitor changes in forest resources and forest cover.
Five. Statistical analyses are not clear and problematic. Did the authors use generalized least squares models for all the response variables? Authors affirmed that was no evidence for spatial autocorrelation because AIC values for non-spatial models were lower than those for spatial models. This is a wrong way of testing spatial autocorrelation and the references (Yuan et al., 2019; Chun et al., 2020) provided are from the same team of authors and cannot be used to justify this. Please provide the Moran’s Index test statistic for each of the models. Looking at the environmental data, there is no information on the grid of the soil and climatic data collected. Obviously, we expect strong spatial components here looking at the smaller plot size. This reinforces the need for appropriate spatial autocorrelation test.
Six. Still in the statistical analyses sections, there is no need to transform predictors, what we are interested in is the distribution of the residuals of each model. Please provide this information along with the shapiro-wilk test to cross-check how normality and linearity were improved as you stated in line 164.
Further, with the variation of the age class of the plots, why was age not considered in the analyses? With age being left out, I do not think the analyses conducted here bring any reliable conclusion of ecological processes as described in the manuscript. Also, the whole section on the statistical analyses need to be revised to link to each hypothesis/research question. As it stands, it is very bulky and one could not know exactly which analyses are responding to which question/hypothesis.
Seven. The rationale for the piecewise SEM is not provided, and I am not sure if you can test the indirect effects with piecewiseSEM as you stated in line 189. If yes, please explain this. I know lavaan has a clinical way of doing this based on global estimation, but I think pSEM is more of local estimation with sub-set models. Again, authors need to present the results of these sub-set models (not as graphics as it is now in the appendix). What are the different sub-set models? This is even more critical since you have multiple response variables here, and we do not know if all of them were fitted with the same type of model. Please ensure that you report statistics appropriately, with respect to your questions, from the different models tested. Please provide R codes for us to counter check accuracy of these results.
Eight. Today, what we are interested in is a more biological link that explains the results. Yes SEM has been widely used in BEF studies, but it is not a pass code. They only provide "causal links" and we should go beyond significant SEM links. Trait-based modeling or experiment, but statistical analyses like these will not provide robust findings, rather showing the obvious!
Below are my specific comments
Abstract
Line 16: which forest processes are the authors referring to? Are those forest processes being studied here? If yes, please provide details
Line 17: 20 to 50 years age of stand provide considerable variance for you to consider the effect of age in the analyses. I suggest that effect of age be considered here
Lines 15- 20. Logic is missing here. First provide the background and gap of the study, then the objectives/hypotheses to address the gap, and after the method/sampling design used.
Line 20: Why did you consider the effects of functional diversity, functional dominance of traits, stem density, and abiotic drivers? You did not provide any background to this
Lines 23-25: Nothing new here
Line 27: self-thinning? Please moderate your stance
Lines 28-29: How can we be convinced about your conclusion on the effect of large trees across forest strata, when you only studied stem with > 6 cm dbh. Does this make sense?
Line 29-31: above ground biomass if far from telling us a complete story on ecosystem function. So please again avoid un-founded conclusions
Introduction
Line 35: what do you mean by the “mechanisms of biomass dominance”?
Line 37: “carbon sequestration is distributed”?? Please revise
Line 33-43: This first paragraph lacks logic in the succession of ideas: in the same paragraph, you introduced in this order, large-diameter trees, mechanisms of biomass dominance (which you did not explain), carbon sequestration in younger trees, forests potential for carbon stock. Please revise this to provide more logic as you introduce an idea at the beginning of your paragraph
Line 44 -48: You are not saying anything relevant here. At least, I expect that you provide state of art background on the contrasting effects of abiotic factors on AGB, rather than just citing them.
Line 48-50: for consistency, I expect that you give exemple of biotic factors, and how they affect AGB.
Line 50-51: Please revise this. Not well stated
Line 52: What about the selection effects? Please explain how the mass-ratio is linked to selection/sampling effect
Line 82-84: why not in the understory? Please expand futher
Line 84-86: The hypotheses are not specific here. Please provide expected direction of the effects. Is aridity not derived from other climatic factors?
Line 87: Which edaphic factor? And how?
Material and Methods
Line 105: Actually, authors combined 4 subplots of 0.04ha to make the 0.16ha. How confidently can we assess large size trees in 0.04 ha subplot. The observation unit is too small for this kind of study.
Line 115-116: It is no acceptable to talk about understory when you have only considered tees with dbh>6cm
Citation: https://doi.org/10.5194/bg-2022-60-CC1 -
RC2: 'Comment on bg-2022-60', Anonymous Referee #2, 08 Dec 2022
Chang-Bae Lee e al. produced a manuscript on Large-diameter trees and forest structure and function in successional temperate forests.
The authors made use of existing 1,956 0.16 ha plots from the Korean National Forest Inventory from mostly 20–50 years old stands (biomass accumulation phase) in closed canopy temperate forests, with 236 species of woody plants and 391,543 individual stems ≥ 6 cm diameter at breast height.
Overall, the authors found that large-diameter trees had a dominant effect on AGB compared with remaining tree attributes and abiotic drivers for both the overstory and whole community; but not in the understory. I have noted several issues and flaws in this paper, which should be reconsidered by its authors. Prominent ones are the similarity with previously published papers by the same team and lack of knowledge gap, sampling inappropriateness, and statistical/reporting mistakes. The current manuscript is not suitable for publication.
After reading the whole manuscript, I think there is a disconnect between the title and the subject of study here. I do not believe that a study of biomass (aboveground biomass) is sufficient for authors to generalize this to forest functions. Aboveground biomass alone is not enough to provide generality on ecosystem functions. Please revise the title to reflect what is being studied in this paper.
Second, I am not convinced that temperate forests in Korea are representative samples of temperate forests across the globe. So please again revise the title for more specificity.
I did not see any new insights from what we already know and that the same team of authors have previously published. Where is the knowledge gap here? Authors talked about forest succession, but did not even account for the successional stages in their analyses. On the contrary, the authors have just endorsed findings from most previous studies, and just to mention the initial papers by (Lutz et al. 2012; Lutz et al. 2013) and the few papers below:
Lutz et al. 2018. Global importance of large-diameter trees, Glob. Ecol. Biogeogr., 27, 849–864, https://doi.org/10.1111/geb.12747
Ali et al. 2019 Big-sized trees overrule remaining trees’ attributes and species richness as determinants of aboveground biomass in tropical forests, Glob. Chang. Biol., 25, 2810–2824
Ali, A., et al.2020 Big-tree–energy mechanism underlies forest diversity and aboveground biomass, For. Ecol. Manag., 462
Ali, A., and Wang, L. Q. 2021: Big-sized trees and forest functioning: current knowledge and future perspectives, 360 Ecol. Indic., 127
Yuan, Z., Ali, A., Sanaei, A., et al. 2021 : Few large trees, rather than plant diversity and composition, drive the above-ground biomass stock and dynamics of temperate forests in northeast China, For. Ecol. Manag., 481
I did not see much difference between these papers and the manuscript presented here. All of what is described in this manuscript have appeared in different forms in many of the above papers. It is hard to see the specific advance here. The authors need to do a much better job in presenting the novelty and the added value in this manuscript, else, I see this more like a replication or a “cookie cutter” of previous studies with no much scholarship on its own. This also applies to the arguments, and analytical methods presented in this manuscript. Linked to the latter, I point out my additional major concerns:
First. The study failed to be more analytical to avoid linear testing of the effects of “part of the sum”. Their definition of large-sized trees is based on the largest 1% tree in each plot. As such, there is no other alternative for large sized trees than to be the most determining factor here, because they represent the big part of the sum. Even in plot with lowest AGB, you will still have relatively bigger tree (see line 130, where you had the large-diameter threshold varying from 12 cm to 91.5 cm) that forms part of that plot biomass. So this means that in each plot you will see that large size trees contribute highly to AGB. So do we expect otherwise? It would make a bit of sense, if large-size trees were determined at community level (i.e. across all plot), then used to differentiate for each plot. Again, be careful of the metric being used because of the potential circularity and high collinearity.
Second. Authors said they used 1956 plots of 0.16ha (line 16). In lines 105-107, they made use of 4 plots of 0.04ha each. This means that the initial sampling unit was not 0.16ha, but 0.04ha. How can we really assess large-sized trees and forest structure in plots of 0.04 ha (20x20m), which are much convenient for herbs/phytosociology/releve survey. Although they have combined 4 plots of 0.04ha to make it 0.16ha, this remains a flaw because initial sampling units cannot just be aggregated to form analytical units, without proper accounting for hierarchical/nesting methods.
Third. The designation of understory here is also problematic. In line 106, they have only considered trees with dbh >6 cm, ignoring all plants in the < 6cm dbh classes. As such, it seems that the true contribution of the understorey is being ignored here. So how can we talk about understorey when trees in class of < 6 cm dbh are not considered. This is a methodological flaw that needs to be addressed in the analyses. It is further strange that authors did not consider wood density as a relevant trait here for biomass, but used seed mass???.
Four. From my last two comments, it is clear that the sampling design is not appropriate for this study, or at least for the research questions. As we all know, national forest inventories are primarily carried out for purposes other than assessing biodiversity-ecosystem function relationship and I am very critical of studies that use samplings that are not initially designed for a given study. In fact, in lines 101-102, authors state that the NFI protocol has been designed and implemented to monitor changes in forest resources and forest cover.
Five. Statistical analyses are not clear and problematic. Did the authors use generalized least squares models for all the response variables? Authors affirmed that was no evidence for spatial autocorrelation because AIC values for non-spatial models were lower than those for spatial models. This is a wrong way of testing spatial autocorrelation and the references (Yuan et al., 2019; Chun et al., 2020) provided are from the same team of authors and cannot be used to justify this. Please provide the Moran’s Index test statistic for each of the models. Looking at the environmental data, there is no information on the grid of the soil and climatic data collected. Obviously, we expect strong spatial components here looking at the smaller plot size. This reinforces the need for appropriate spatial autocorrelation test.
Six. Still in the statistical analyses sections, there is no need to transform predictors, what we are interested in is the distribution of the residuals of each model. Please provide this information along with the shapiro-wilk test to cross-check how normality and linearity were improved as you stated in line 164.
Further, with the variation of the age class of the plots, why was age not considered in the analyses? With age being left out, I do not think the analyses conducted here bring any reliable conclusion of ecological processes as described in the manuscript. Also, the whole section on the statistical analyses need to be revised to link to each hypothesis/research question. As it stands, it is very bulky and one could not know exactly which analyses are responding to which question/hypothesis.
Seven. The rationale for the piecewise SEM is not provided, and I am not sure if you can test the indirect effects with piecewiseSEM as you stated in line 189. If yes, please explain this. I know lavaan has a clinical way of doing this based on global estimation, but I think pSEM is more of local estimation with sub-set models. Again, authors need to present the results of these sub-set models (not as graphics as it is now in the appendix). What are the different sub-set models? This is even more critical since you have multiple response variables here, and we do not know if all of them were fitted with the same type of model. Please ensure that you report statistics appropriately, with respect to your questions, from the different models tested. Please provide R codes for us to counter check accuracy of these results.
Eight. Today, what we are interested in is a more biological link that explains the results. Yes SEM has been widely used in BEF studies, but it is not a pass code. They only provide "causal links" and we should go beyond significant SEM links. Trait-based modeling or experiment, but statistical analyses like these will not provide robust findings, rather showing the obvious!
Below are my specific comments
Abstract
Line 16: which forest processes are the authors referring to? Are those forest processes being studied here? If yes, please provide details
Line 17: 20 to 50 years age of stand provide considerable variance for you to consider the effect of age in the analyses. I suggest that effect of age be considered here
Lines 15- 20. Logic is missing here. First provide the background and gap of the study, then the objectives/hypotheses to address the gap, and after the method/sampling design used.
Line 20: Why did you consider the effects of functional diversity, functional dominance of traits, stem density, and abiotic drivers? You did not provide any background to this
Lines 23-25: Nothing new here
Line 27: self-thinning? Please moderate your stance
Lines 28-29: How can we be convinced about your conclusion on the effect of large trees across forest strata, when you only studied stem with > 6 cm dbh. Does this make sense?
Line 29-31: above ground biomass if far from telling us a complete story on ecosystem function. So please again avoid un-founded conclusions
Introduction
Line 35: what do you mean by the “mechanisms of biomass dominance”?
Line 37: “carbon sequestration is distributed”?? Please revise
Line 33-43: This first paragraph lacks logic in the succession of ideas: in the same paragraph, you introduced in this order, large-diameter trees, mechanisms of biomass dominance (which you did not explain), carbon sequestration in younger trees, forests potential for carbon stock. Please revise this to provide more logic as you introduce an idea at the beginning of your paragraph
Line 44 -48: You are not saying anything relevant here. At least, I expect that you provide state of art background on the contrasting effects of abiotic factors on AGB, rather than just citing them.
Line 48-50: for consistency, I expect that you give exemple of biotic factors, and how they affect AGB.
Line 50-51: Please revise this. Not well stated
Line 52: What about the selection effects? Please explain how the mass-ratio is linked to selection/sampling effect
Line 82-84: why not in the understory? Please expand futher
Line 84-86: The hypotheses are not specific here. Please provide expected direction of the effects. Is aridity not derived from other climatic factors?
Line 87: Which edaphic factor? And how?
Material and Methods
Line 105: Actually, authors combined 4 subplots of 0.04ha to make the 0.16ha. How confidently can we assess large size trees in 0.04 ha subplot. The observation unit is too small for this kind of study.
Line 115-116: It is no acceptable to talk about understory when you have only considered tees with dbh>6cm
Citation: https://doi.org/10.5194/bg-2022-60-RC2
Viewed
| HTML | XML | Total | Supplement | BibTeX | EndNote | |
|---|---|---|---|---|---|---|
| 1,073 | 401 | 63 | 1,537 | 117 | 43 | 47 |
- HTML: 1,073
- PDF: 401
- XML: 63
- Total: 1,537
- Supplement: 117
- BibTeX: 43
- EndNote: 47
Viewed (geographical distribution)
| Country | # | Views | % |
|---|
| Total: | 0 |
| HTML: | 0 |
| PDF: | 0 |
| XML: | 0 |
- 1
Cited
Arshad Ali
Zuoqiang Yuan
James A. Lutz
Jens-Christian Svenning
Min-Ki Lee
This preprint has been withdrawn.
- Preprint
(1097 KB) - Metadata XML
-
Supplement
(2229 KB) - BibTeX
- EndNote