the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 04 Feb 2025
Microbial carbon use for incorporating biomass phosphorus drives CO2 emission in phosphorus-supplied subtropical forest soils
Abstract. Subtropical forests store significant amounts of soil organic carbon (SOC) and are important in the global C cycle. Current understandings based on controlled experiments indicate that phosphorus (P) availability promotes SOC decomposition by alleviating microbial P limitation or rendering SOC available for microbial decomposition. While no alternative mechanism is currently known, it is uncertain if this mechanism holds across soils or P supply levels at the field scale. We formulated an alternative mechanism for acidic subtropical forest soils where organic C (OC) is bound to iron (Fe). Our hypothesis proposed that P supply would promote Fe-bound P formation and desorption of OC previously bound to Fe, and the microbial utilization of the desorbed OC for P-cycling contributes significantly to CO2 emission. We tested our hypotheses by utilizing a forest P addition platform to explore C-dynamics, its regulators, and utilization across four P supply levels: 0, 25, 50, and 100 kg P ha-1 yr-1 (Con, P1, P2, and P3, respectively) for one year. Phosphorus supply significantly increased the periodic and cumulative dissolved OC (DOC) concentration, especially in P3, and was associated with increased iron (Fe)-bound P formation. With increased DOC following P addition, microbial biomass P (MBP) significantly increased, while MBC remained unchanged. The significantly positive relationship between MBP:MBC ratio and DOC, significant increase in MBP and carbon dioxide (CO2) emission with P addition, and the reduction in CO2 emission with increasing MBC:MBP ratio (0–10 cm) supports our results that the desorbed-C alleviated microbial C-limitation induced during P-cycling, particularly, MBP incorporation, to drive CO2 emission. Structural equation modeling and multivariate analyses projected MBP as a critical factor inducing CO2 emission. Besides, insignificant alterations in the relative abundance of C-degrading functional genes and reductions in P- and C-degrading enzyme activity indicated the sufficiency of desorbed OC for microbial use without further SOC degradation. Our study provides an alternative mechanism of P's impact on soil C-cycling processes in acidic subtropical forest soils vital for constraining process-based C models.
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Status: final response (author comments only)
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RC1: 'Review', Anonymous Referee #1, 12 Feb 2025
General comments
Authors present an interesting fertilization study from a subtropical forest in SE China. Authors make an interesting hypothesis that P addition would release SOC bound to Fe in the soil, making it available for microbial attack, and explaining higher CO2 emissions under P addition. This hypothesis is presented as an alternative explanation to existing knowledge paradigms. The approach to test the hypothesis included sampling soils at various time points after P addition (2 weeks to 1 year) and measuring soil P pools with Hedley as well as several biological soil properties. The study is potentially very interesting and valuable for the soil science community, but the manuscript needs to be improved significantly.
The quality of the presentation is low and needs to be improved. Most of the figures are incomplete in terms of axes labels or captions, creating a sloppy impression.
The same goes for the statistical analyses, which is not complete / always appropriate. Authors need to perform and report rigid model diagnostics for linear regression and structural equation models.
A suggestion in terms of framing, I recommend authors to use the concept of “P and SOC competition for binding sites”, which I think is a more useful concept to test and explain the observed phenomena.Main comments
From the abstract its not clear how the new hypothesis differs from the established knowledge because both in effect have to do with rendering SOC available for microbial decomposition. Please distinguish old and new hypotheses more clearly.
Authors need to interpret the findings in a more nuanced way, given the limitations of the methods used. For example, in the abstract I read that Fe-bound P was quantified, which made me assume XANES or similar was used—a method that can distinguish Fe-bound P from other P forms. However, from the methods it becomes clear that authors used a sequential extraction. Sequential extraction contains many assumptions and limitations and results cannot be attributed to a specific P form. Authors need to rewrite the manuscript to account for the nuances of the limitations of the approach used.
The section on DOC dynamics needs to be rewritten. Currently the text is not supported by the data as presented in the figures. The text claims that DOC was increased but the data does not show it, or at least it presents a much more nuanced picture.
The linear and structural equation models used are not capturing a lot of the variability, as can be seen in the low R2s. Authors should discuss what unaccounted for variables or what methodological limitations might explain the variability.
I do not have expertise of DNA sequencing approaches so cannot evaluate the quality of that work.
Minor comments
l. 35 introduce abbreviation MBC
The map in Figure S1 should be improved because it is not clear where in Guangdong the experimental site is. Also not clear what the different fill colors of the provinces are supposed to represent.
l. 134 what is the World Reference Base equivalent of the soil type?
l. 158 change “samples collection” to “sample collection”
l. 188 please cite the original reference for this method as well. From the description here it is not clear how the method used (from Hou et al. 2018) differs from the standard Hedley extraction. Please clarify.
l. 192 what justifies assuming that NaOHPi equals Fe-bound P? This is a very shaky assumption in my opinion. It could be fully Al-bound P or a mix of many different P forms…
l. 204 Please mention if a spike was used to correct for sorption. If not, please discuss implications on results.
l. 251 change “supply of increasing P” to “P fertilization” or P input or P addition
Fig. 1 what does the small inset plot with the orange bars show? Axes labels missing I in inset plots. Also, the panel titles (a, b, c, d) are on top of axes labels.
Fig. 2 and 3. Same problem. What is the inset showing?
l. 268 this does not seem to be supported by the results.
l. 272-273 this makes no sense. Please be more nuanced
Fig. 1-3 if using post hoc testing to determine differences between treatments please indicate significant differences with letters on top of the error bars (bar plots)
Fig. 4 linear regression modeling as done here is problematic because the observations are not independent, violating assumptions of linear model. To account for the site and treatment effects, linear mixed models should be used with time point and treatment as random effects.
Linear regression modeling. How was model diagnostics done?
Fig. 5 what about the blue lines?
l. 419-428 why only focus on Fe? What justifies the assumption that Fe-sorption is driving P and C dynamics, as opposed to sorption to Al oxides?
l. 431 see alsoP and Corg competition for sorption sites in Regelink et al. 2015 (European Journal Soil Science)
Fig.7. Also here, why can you assume its all driven by Fe bound and not a mix of Fe and Al (hydr)oxides?
l. 614 the statement needs to be made more precise. All soils are capable of binding anions to some degreeCitation: https://doi.org/10.5194/egusphere-2025-310-RC1 - AC1: 'Reply on RC1', Muhammed Mustapha Ibrahim, 08 Apr 2025
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AC3: 'Reply on RC1', Muhammed Mustapha Ibrahim, 18 Apr 2025
We have supplemented our response on one of the comments raised and addressed in the previously attached document.
Comment
Fig. 4 linear regression modeling as done here is problematic because the observations are not independent, violating assumptions of linear model. To account for the site and treatment effects, linear mixed models should be used with time point and treatment as random effects.
ResponseYou are right. We have reevaluated our observations and subjected our data to linear mixed-effect models to provide more robust relationships among our variables. We used the sampling date as the random factor and obtained more robust R2 values (R2>0.4) compared to the low values previously obtained using linear regression models. We limited the random factor of the linear mixed-effect models to the sampling date because it would most likely capture a large aspect of the variations arising from the differences in soil and climatic conditions during the different times and seasons where sampling was carried out, differences in point of re-sampling, etc. Also, including other random factors like treatment effect could result in overfitting, where the model captures noise rather than the underlying signal and reduces the model's ability to generalize to our data. Besides, understanding the contribution of each random effect becomes challenging and could obscure the practical implications of our deductions from the model. For clarity, we provided the marginal R2 and conditional R2 values in the relevant figures to clearly show the prediction capacity of the fixed effect and its combination with the random effect.
Citation: https://doi.org/10.5194/egusphere-2025-310-AC3
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RC2: 'Comment on egusphere-2025-310', Anonymous Referee #2, 02 Apr 2025
The manuscript of Tan et al. presents a field phosphorus (P) fertilization experiment with measurements of P fractions, DOC and CO2, as well as soil microbial community data. The study thus combines different relevant aspects in the context of C and P cycling in the studied tropical forest soils. The field experiment was thoroughly conducted, including many sampling time points for a field scale.
However, while I agree that P dynamics can influence CO2 emissions, the discussed underlying mechanisms cannot be conclusively disentangled with the provided results. The experiment included only P addition treatments, no C addition or combined C and P addition, therefore, the discussed change in C cycling always occurred in parallel with the change in P cycling. Also, the effects of the P addition treatments on C dynamics are not as clear as suggested (e.g., DOC increase only in P3, not P1 and P2 (Figure 2a), no respiration increase in P1 (Figure3f)), while there was a clear increase in P availability (Figure 1a). The discussed relationships (e.g. DOC and MBP) are mostly minor/inexistent (very low R2 in Figure 4).
As the provided results are not sufficient to support the current mechanism discussion, I suggest shifting the focus rather towards the discussion of the field setting and additional processes relevant at that scale. For example, I was missing a more profound discussion on the effect of tree presence (e.g. P uptake and C exudation) and leaching.
In addition, the statistics presented in the figures are unclear, and some methodological details are not explained or are inconsistent (e.g. P fraction methodology and naming/presentation in figures). Also, the manuscript would profit from streamlining the text (introduction and discussion are long and sometimes repetitive).Please find below some more specific comments:
Material & Methods
L. 134: “latosol red soil”, in which soil classification system? Instead of giving the equivalent in the US system, it might be more universal to give the equivalent in the WRB system?
L. 143: Where can we find the basic nutrient concentration data?
L. 184 Chapter title “Samples analyses” is very broad, I suggest dividing this part into several chapters, separating the quite different analyses.
L. 193 and 207: Please be more precise regarding the methods. Malachite green method is used to determine phosphate/inorganic P in different extracts. This can be done for different pools and is not necessarily available P. E.g. instead “Inorganic P in xx and xx extracts was determined using Malachite green”. Also, for microbial P there needs to be an extraction step before measuring P by the Malachite green method. How was this done and was this step part of the sequential extraction or not?
How did you determine the organic P concentrations (NaHCO3 Po and NaOH Po)?Results
L. 252 and Figure 1: In the method section you described a modified Hedley extraction including resin Pi but not the Bray extraction that seems to be behind the “available P” discussed here. Why are you not showing the resin Pi when you then use the other pools from the sequential extraction (NaOH Pi)? If the Bray extraction was used this needs to be added/adapted in the method section.
Figure 1 (also applicable to other Figures): For the inserted small plot (barplots in general), it is not clear from the plot which treatments differed from each other. The statistics were done only for the average over time (inserted small plot), or? Also, the p-value in the plot is different from the p-value in the Figure description.
L. 316- 341 and Figure 4: Even if the relationships have significant p-values, some of the R2 are very low (< 0.1), and I would be more careful interpreting these relationships. To me, these figures mainly show that there is a lot of variability, as expected in a field setting. Also, if you discuss the soil horizons separately, please give the R2 for the relationships per horizon, not only the p-value.
Figure 5: What are the additionally added R2 representing here, they seem not to match the r given for the connections. Fe-P is mentioned in the description but not shown.
L. 389-392: Yes, but in the detailed analysis with linear models in Figure 4 these patterns are not conclusive.
Figure 6: Why did you in the RDA (Figure 6h) include CO2 together with the genes as target variable while the other chemical variables are used as explanatory variables?
L.387: The mantel test seems mostly useful to target the relationship between different datasets (genes and soil properties), so to me it is unclear why this analysis is used here to focus again on the correlations between CO2 and MBP, Ap, Fe-P (more detailed in Figure 4) and not to explain the links between genes and soil properties.Discussion
L. 453-455: Please check sentence logic; if BG activity decreased, it was not responsible for the breakdown of organic C and increase in DOC?
L.461-464: There might have been no increased uptake/use of C by microbes but rather leaching of DOC?
L. 464-466: “MBP increased with increasing DOC concentration”: I was not able to find a visualization of this relationship, except for the rank correlation in Figure 6g, where the correlation seems inexistent/minor and the SEM model in Figure 5 (r=0.14). This relationship would need to be shown more clearly for this conclusion. I agree that there is a cost of C for microbes, but MBP also increased with P addition (Figure 1), and this pattern seems stronger, so MBP might just follow P availability. Indeed, in your SEM model, the link between available P and MBP is stronger (r= 0.38) than between DOC and MBP (r=0.14). To be able to conclude that DOC increase is the main pathway increasing MBP, a treatment with DOC increase but no P addition would be needed.
L. 487-489: From the presented results, it is not clear that the microbes were C-limited; you would need to explicitly check the effect of C addition to conclude that.
L. 505: If you refer to the SEM model in Figure 5, Fe-P is not included there.
L. 519-521: Or again, this has to do with the higher P availability itself.
L. 594-595: Where do you show the leaching of DOC? The results focus on 0-20 cm DOC contents in soil; leaching itself was not shown in the manuscript/figures.Citation: https://doi.org/10.5194/egusphere-2025-310-RC2 -
AC2: 'Reply on RC2', Muhammed Mustapha Ibrahim, 18 Apr 2025
We appreciate the referee's in-depth review of our manuscript. It has enabled us to improve the manuscript's content, structure, and, most importantly, to present the obtained results more accurately and objectively. We have attached a detailed response to the referee's comments, which were done on a point-by-point basis.
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AC2: 'Reply on RC2', Muhammed Mustapha Ibrahim, 18 Apr 2025
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