Influence of Long-Term Soil Management Practices on Carbon Emissions from Corn (Zea mays L.) Production in Northeast Croatia
Round 1
Reviewer 1 Report
Comments for author File: 
Comments.pdf
OK
Author Response
Dear Reviewer,
You will find our responses to your comments below in Microsoft word document.
Sincerely,
The authors
Author Response File: Author Response.pdf
Reviewer 2 Report
The manuscript is a well-edited thorough work. It deals with an important problem, and the chosen experimental methods can contribute usefully to the achievement of the set goals. But they can't give an answer.
And this is one of my main objections to this paper. The title of the thesis refers to the study of carbon sequestration. CO2 emission can be found in the objective, and the results CO2 emission measurement are in the manuscript. However, the relationship between CO2 emissions and carbon sequestration is not clear at all. No tests were carried out to measure the amount of carbon remaining in the soil. No estimates, even though e.g., the root mass of maize could be estimated, even based on the crop yield data. Or the mass of straw can be a useful parameter.
In the absence of these measurements (or estimates), it is not possible to state which treatment (mineral fertilization, organic fertilization, unfertilized) has a more favourable effect in terms of the carbon cycle, because only CO2 emissions were measured. And even the treatment with the highest emission value can be good if the carbon sequestration is also high (which we don't know here).
I recommend that, in addition to evaluating CO2 emissions, the process and importance of carbon sequestration should also be mentioned in the manuscript. And in the title should be co2 emission instead of sequestration.
My other main objection concerns the interpretation of the results. The measurement results and their statistical evaluation were correctly described in the Results chapters. Based on the statistical evaluation, the effects are most often either not significant or not important. In the Discussion chapter, this assessment is not taken into account, and in the Conclusions, it is not even mentioned that the described findings/statements are not significant. So, reading only the conclusion or the abstract will mislead the reader. Unfortunately, often only these parts are read. In this research work bare fallow was a kind of treatment. It was really useful, and gave statistical differences, but in the evaluation is not entirely correct (it’s a bit misleading) to refer it as a management practice, like fertilization.
I recommend revising these two chapters (Discussion, Conclusion) so that the statistical uncertainty of the findings is presented. Which, by the way, is completely normal, especially in a field experiment, where it can only be reliably evaluated on the basis of many years of data series.
My comments on the details are listed below:
Introduction:
line 63: “emission uptake” What does it mean?
Materials and Methods:
in Table 1: amounts of p2O5 and K2O. Available or total concentrations are given? If available, according to which method? Maybe providing data about water holding capacity would be useful. The weather data of the intervening years are also important, or instead of the water content of the soils in the beginning month of the experimental year.
in line 122-123: AL-soluble available P2O5, K2O or anything else?
Results:
in line 221: just for the sake of interest, it would be worth investigating whether the soil moisture data correlates with the precipitation data (this is not an official suggestion)
I think so Table 3 and 4 are unnecessary, their content can also be reported on the appropriate figures.
in Table 3 and 4: the number of decimal places is too many; the sign of x in the equation does not correspond to that in the figure
Discussion:
in line 314-315: “soil moisture was 23.41 mm” mm is not a proper unit here
Conclusion:
in line 349: “carbon sequestration” This is the first occurrence of this term. It should be discussed earlier.
Best regards,
Author Response
Dear Reviewer,
You will find our responses to your comments below in Microsoft word document.
Sincerely,
The authors
Author Response File: Author Response.pdf
Reviewer 3 Report
GENERAL COMMENTS
This study fits perfectly within the scope of the journal “agronomy” and fulfils the purpose of studying the effects of soil management on carbon emissions within a specific agronomic production.
Explicitly, the authors have conducted a field study in Popovaca (central part of Croatia), during the period 2013-2015-2017, taking as climatic reference the period 1991-2020, in a pedogenic context of stagnosols (WRB 2006-2007).
Four treatments with four repetitions (including control plot) of experimental plots, 30 × 130 m² in size, were carried out. The distance between treatments was 2 m on each side. Soil properties were determined in composed soil samples obtained from the top layer. Soil analytical procedures followed the HRN ISO methodologies. The C-CO2 flux was measured in these plots six times per year (three replications by plot), following the in situ closed static chamber method, with the appropriate calculations. The study of data was performed with ANOVA, and tested with a post-hoc (Fisher) t-test at a significance level of 5%. Additionally, a regression analysis was used to stablish relations between soil carbon flux and soil temperature/moisture for each of the three years of the studied period, from April to October.
I found that, in general, the paper is ordered, well developed and well exposed, and the methodology is correct although should be expanded a bit. Consequently, the authors reach results that should be made available to the scientific community. However, there are some explanatory insufficiencies and the English expression needs an overhaul by a native English speaker. Although this research is worthy of consideration for publication in this journal, I believe that this study should be improved in some aspects that prevent it from being published in its current form.
MAIN CONCERNS AND QUESTIONS
1-In general, I observe that the Title include the concept “sequestration” but this term is only mentioned 5 times in the manuscript (2 times in the Title and Conclusions, and 3 times in the References). However, the concept “emission” has been used 82 times (20 in the references). I suppose that the authors agree with me that these concepts are different, and the paper is much more about the emissions (what soil releases into the atmosphere) than sequestration (how GHG are captured in the soil). If this approach is correct, the reader misses an explanation of this imbalance. In my opinion, this paper really researches CO2 emissions from the soil, and it is very easy to improve this “involuntary” mistake.
2-I am not sure if the authors intend to state the actual influence indicated in the present title, or to leave it more open-ended, with a title similar to “Influence of long-term soil management practices on carbon emissions from Zea Mays L. production.”
3-The authors do not clearly state throughout the manuscript what is the origin of CO2 emissions from the soil: the reader often observes that attempts are made to stablish relationships between temperature/moisture and CO2 emissions, but the reader cannot find a working hypothesis in this regard. I also miss a description of the Ap-horizon as a possible main source of gases: this horizon should be the richest horizon on organic matter, although part of this CO2 can have a net biological origin (plant respiration, microorganisms). Additionally, in this context, what role do the lower soil horizons (>10 cm) play?
4-It would be interesting to indicate explicitly if the samples were sieved, and what mesh was used. The same occurs with pH determinations (giving the water/soil ratio), and whether the Robinson pipette was used to establish soil textures, etc.
Perhaps this information is contained in the indicated protocols, but this should be clearly stated to facilitate future comparisons for other researchers.
5-Ls149-151. Please, explain a bit more how the determination of soil moisture were made.
6-Section 2.6. The ANOVA analysis has requirements that must be met. Although this sounds routine, nothing is indicated on this point, and this protocol must be followed. The authors should not forget that this statistical methodology only gives pragmatic results, and does not go to the point of the problem.
7-Ls228-229. I agree with the authors that these relations are very weak, but it seems that the better related correspond to that of 2015. Please, revise and explain better.
8-Discussion. The authors should use their own data, and therefore should appear their auto-references in this section: I don’t see references to any Table, and it only appear auto-referenced the Figure 1 (L295). For instance, in Ls283-287 they refer to data that is based by their own determinations, but don’t appear this reference: this would give consistency to their own determinations. Please, improve this issue.
9-Ls304-305. The authors state that CO2 emissions are a complex issue and indicate one reference. Ok, but I advise writing at least one more reference and briefly indicating some of these factors and some commentary.
SPECIFIC COMMENTS
Throughout the text:
I advise writing dates following the Anglo-Saxon system: 02/05/2013.
It is confusing the use of the “acronyms” such as “Mineral F.” or “Organic F”. However, the authors write “Black fallow” without an acronym. Please, be consistent and clarify.
Isolated points:
L21. I believe that the high increment indicated deserves a very brief comment.
L68. Please, give the Soil Classification System used, and the year. For instance, Stagnosols (WRB, 2014), as well as its reference number.
L69. The reader should assume that the information contained in Table 1 is referred to the Ap horizon. Similarly, the depth included refers to the “total” soil depth. Please, clarify.
L73. I suggest writing “… are presented on …”
Ls73,90,93. I advise writing “... throughout the reference period (1991-2020) …”
L102. It is simpler writing “four treatments were studied”
L118. It is more appropriate to write: “Laboratory determinations”
L129. What do the authors understand by “each vegetation year”? This should be clarified.
Expression in English is acceptable, although proofreading by a native English speaker would be helpful.
Author Response
Dear Reviewer,
You will find our responses to your comments below in Microsoft word document.
Sincerely,
The authors
Author Response File: Author Response.pdf
Reviewer 4 Report
Dear Authors,
Comments in the attached file.
Best regards,
Comments for author File: Comments.pdf
Dear Authors,
Comments in the attached file.
Best regards,
Author Response
Dear Reviewer,
You will find our responses to your comments below in Microsoft word document.
Sincerely,
The authors
Author Response File: Author Response.pdf
Round 2
Reviewer 1 Report
Review of ‘Long-term soil management practices influence carbon sequestration in Zea mays L. production’
I regret to say that my criticisms of this paper as originally presented still stand. Figs 5 through 10 have been replaced by new sets of figures that show the same results as before (even though the data plotted seems to be different); that is, there is only one significant regression of CO2 flux against temperature or soil moisture, and even that has a very low R2 value, as before. The data for the various treatments over the three years appear to be random. As I said before, this must be because there is great variability in the measurements of CO2 flux, which is not unexpected given that such a small area of each treatment plot was sampled to measure the flux on each occasion. I calculate that for three sample measurements in each plot of 3584 m2, the sample area was only 0.004 percent of the whole plot area. The emission flux of CO2 from a soil is likely to be spatially very variable, hence the large variability if the data.
Thus, on reflection I think the only meaningful graph is that of Fig. 3 where now the overall average emission flux for each treatment in each year is shown. This tells us that only the emissions from Bare Fallow differed from the other average fluxes in two out of the three years.
One minor point. The concentration of CO2 measured under the dome cannot have the units of micromoles-1 in the equation on l.175. If this were so the dimensions of this equation would not come out as mass per unit area per unit time. In the preceding paragraph the authors refer to the concentration in ppm.
Language required minor editing only
Author Response
Dear Reviewer,
Thank You very much for the time that You have taken to review our paper. Bellow, in Microsoft word document, You will find our responses to your comments.
Sincerely,
The authors
Author Response File: Author Response.pdf
Reviewer 2 Report
The authors modified the manuscript according to the comments. The mentioned inaccuracies have been corrected. The revised manuscript meets the requirements of Animals.
Best regards
