This reviewer strongly supports the type of research that the authors present in their paper: characterize field conditions on soils where certain management types have been applied for a substantial period. The authors also present a professional paper in terms of methods used, particularly the method to measure retention curves ,and by applying multiple experiments and proper statistical analyses.

Unfortunately, when they conclude in the end that: “the study contributes to higher sustainability of mediterranean agrosystems”, they are off the mark. Sustainable development is  defined as having economic, social and environmental dimensions as expressed by the UN Sustainable development Goals (SDG) and the associated European Green Deal. Scientific papers published in 2022 that suggest a link with sustainable development cannot ignore these developments in the scientific, policy and public arena’s. The title of the paper is also  highly misleading: “improvement of cultivated soil” cannot be based only on: “water retention curves”. Numerous published papers describe a systems analysis based on the interaction between soils-water-atmosphere-plants that is needed to assess effects of soil management.

Sustainable development implies for agriculture at least: production of healthy food ( SDG2&3), protection of ground- and surfacewater quality (SDG6), carbon capture and reduction of greenhouse-gas emission (SDG13) and increasing biodiversity and combatting land degradation (SDG 15). 

I would recommend that the authors frame their results in a SDG context: 

1.    It should not be too difficult to report crop yields. (SDG2&3) 

2.    Water tables may be deep and not polluted; this could be mentioned showing that groundwater quality is not really an issue here.(SDG6) 

3.    Carbon capture is not evident as the %C is about the same for OPM and CM. This is interesting because OPM management is supposed to lead to higher %C and their results indicate this may apply to soils in humid regions ,as reported in literature, but not in arid climates. Effect of high temperatures? But.. data only are restricted to 30 cm depth. (SDG13)

4.    Even though the carbon content of both treatments is about the same, the biological soil properties seem to differ. Biodiversity in OPM is higher. This result is interesting because information on soil biology is often missing in other publications and could be part of the main text here and not be presented in an appendix.  (SDG15)

5.    As bulk densities of the two treatments are about the same for 0-5 cm dept and for the 0-30 cm depth( how was the latter measured, we read only the method for 0-5 cm? Effect of high tempera) there seems to be no negative effect on soil structure by CM management which is usually assumed to take place. Big problem here is that analyses were only made to 30 cm depth and a plowpan may well form by CM management but usually occurs at 30 cm depth and deeper. Indeed, as the authors mention on line 320: deeper soil layers are needed. For a correct analysis soils should be analysed for the total rooting depth. (SDG15).

Some additional notes:

1.    Line 45: to study soil pores, morphological analyses are most useful, if only because different types of macropores can be distinguished: e.g. channels of roots or animals or cracks . Deriving pore sizes form moisture retention data is an indirect, approximate  method. Later ( lines 260, 266) micromorphology is mentioned. That should also be done upfront.

2.    Line 190: no significant compaction? Could be deeper in the CM soil, see comment above.

3.    Line 319: infiltration at the surface is mentioned in the context of the pore analysis. But infiltration rates can be measured and this is very important for the Mediterranean environment , certainly when considering climate change where showers will become more intense. CM has more macropores, so the authors suggest that infiltration rates would be higher than  in OPM with fewer macropores. But the CM soil is less stable so crusts may form rapidly, the more so since there are no cover crops and crop residues are removed. So just linking the occurrence of physically derived macropores to infiltration rates is unrealistic without measurements of such rates. In fact, the reasoning should be reversed: measure infiltration rates and then explain differences by looking at pore patterns. 

4.    The authors conclude that more water is stored in the OPM treatment and this should be favorable for plant growth. But this is a statement based on  static moisture retention measurements while storage is determined by in- and outflow from a certain soil volume, a dynamic process as is the moisture supply to plants. Numerous dynamic simulation models are available to quantify this process, that needs hydraulic conductivities of the soil. The authors seem to be unaware of modern soil physical theory. 

5.    As the soil index by Dexter does not provide any valuable results ( lines 226, 317) it should receive much less attention and might as well be omitted. 

A possible new title might be: Effects of innovative soil management on topsoil properties of a Mediterrenean soil. This could focus on several interesting results identified above. Again, I would recommend they would frame their  story in an SDG context. 

The authors should realize that OPM is, in fact, a form of regenerative agriculture, studied in the USA. I recommend that they check with the National Soil Health Institute website. info@soilhealthinstitute.org.  

J.Bouma.

General comments:

The purpose of the manuscript is a simple comparison of the influence of two management systems, conventional cropping and direct-drilling rain-fed cropping in the physical properties of a soil in the north of the Spain. The selected physical properties are the S index of Dexter (2004) and the size distribution of the stable aggregates. Neither the objectives nor the methods represent a new contribution to the fields of Agronomy or Soil Science.

Nevertheless, the relevance of reduced tillage systems for the Mediterranean countries, and the long duration of the field trials, deserve an opportunity for the authors after a thorough revision of the manuscript. Some recent contributions as, for instance, Or et al. (2021) could be inspiring for such a revision.

The Introduction section does not contain a comprehensive, updated perspective of the conservation agriculture and the quality of the soil. Consequently, the objectives, (lines 77-82) are very imprecise.

The Material and methods section is rather incomplete, with some inaccuracies that will be commented later. The climate properties of the study zone are missing. The description of the soil is limited the mention of the subgroup in the Soil Taxonomy scheme, the textural class of the upper soil horizon and Tables 1 and A1. No explanation is given in the text of the methods followed for the determination of the data of Table1. However, the details of the soil water retention in subsection 2.2 and of the aggregate size fractionation in subsection 2.4 are excessive including Figure 1.

The Results and discussion section is incomplete as well. The authors have chosen the van Genuchten soil water retention equation, but, in addition to the absence of the fitted values of its parameters in the text, one misses some consideration of other alternatives as, for instance, the multimodal equations, which according to Jensen et al. (2019), can reflect better the effects of management systems in the soil properties. I have expected some changes in properties like the bulk density, and the presence of some surface crusts, but, apparently, they were not found. The Figure 3 could not give an adequate information on the size distribution of the pores since it is estimated from the soil water retention curve through equation (2). The discussion of the results is fragmentary.

Specific comments

Line 18: instead of ‘unit’ it must be written subgroup.

Lines 25 and 26: ‘significant differences’ must be replaced by a statistic parameter.

Line 28: what is ‘the studied depth’?  

Lines 33-38: The paragraph should be rewritten to improve its comprehension.

Lines 45-47: The sentence is very similar to that of the lines 37-38.

Lines 51-53: The definition of the soil water retention is very imprecise. Why soil water retention ‘is mainly associated with the porous system’ ‘at low suctions’?

Line 56: The treatment of the air entry state is, again, imprecise. The term ‘so-called’ is unnecessary.

Lines 67-70: This paragraph is unclear.

Lines 71 and 77: The two sentences are almost repeated.

Line 85:  for the sake of precision write ‘subgroup’ instead ‘type’ and mention the Soil Taxonomy.

Line 86: The textural class should be silt loam, according to the particle size information of Table A1, where it was correctly indicated.

Lines 88-90: A more complete description of the soils should have been very helpful to understand their behavior. One cannot trust ‘the visual inspection’ to affirm that the soil is homogeneous. As in the line 28, could ‘the study depth’ be defined?

Line 105: The term ‘coverer’ is very odd.

Table 1: The evaluation method must be indicated in the text and the relevant details like the soil-water ratio for the suspension in the measurement of the pH and of the electrical conductivity.

Line 129: Use ‘matric component of soil water potential’ instead of ‘hydric potential’ to be more precise.

Lines 132-133: To establish the relationship between the gravimetric and volumetric water contents, one only need to know the bulk density of the soil. The sentence is confusing.

Lines 142-145: I could not find equation (1) in the article of Dexter (2004a). In fact, I cannot find the relation of this equation with the van Genuchten (1980) equation.

Lines 150-154: The equation was not proposed by Jurin (1718) as one can check reading such an article. Jurin described his observations in that contribution, but the equation was later formulated by Young and Laplace. This equation is usually known as the Young-Laplace equation (e.g. Adamson, 1967, § I.10).

Line 154: Is the (soil water) potential is mentioned, the sign should be negative. The term ‘suction’ is more appropriated here if the symbol ‘h’ has been used for the ‘height’ in the line 152.

 Line 195: The term ‘water capacity’ was already defined, at least, by Arnold Klute in 1952.

Line 196: How ‘field capacity’ is defined in the text? This term must be precisely defined.

Table 2: as indicated above the soil water potential is negative.

Lines 231-233: If the authors are using a structural index, they should not compare the texture but the structure of the soil.

Line 306: The term ‘capillary/available water’ is misleading.

Line 322: I do not think that tillage should be ‘suppressed’. The natural consolidation of the soil surface might be alleviated by occasional shallow tillage operations.

Technical corrections:

Line 54: Writing ‘saturated’ soil is enough.

Lines 146-147: The use of the acronym ‘SUHC’ is needless.

Lines 160 and 364: The correct name is Elliott.

Line 280: The Table reference is A1, not ‘S1’.

Line 235 and caption of Figure 3: The proper adjective is logarithmic.

Incomplete references: Lines 366, 369-370, 373-374, 381, 387-388, 391, 407, 419.

The reference of lines 441-442 is not mentioned in the text.

References:

Adamson, A.W. 1967. Physical chemistry of surfaces. 2^nd ed. Wiley-Interscience. New York.

Jensen, J.L., Schønning, P., Watts, C.W., Christensen, B.T., Munkholm, L.J. 2019. Soil water retention: Uni-modal models of pore-size distributions neglect impact of soil management. Soil Sci. Soc. Am. J. 83: 18-26.

Klute, A. 1952. A numerical method for solving the flow equation for water in unsaturated materials. Soil Sci. 73: 105-116.

Or, D., Keller, T., Schlesinger, W.H. 2021. Natural and managed soil structure: On the fragile scaffolding for soil functioning. Soil Till. Res. 208, 104912.

The authors aiming for comparison of different regenerative soil management systems in comparison to conventional managed systems. They use various measures of soil structure and water retention to evaluate the quality of the management options. The topic is highly relevant for the adoption of cropping systems to climate change.

Unfortunately, the quality of the study does not convince me to suggest a publication in SOIL. The study is very weak in terms of field replications and study sites that leading in total to 6 samples. The analytical tools are basic and provide no innovative approaches. For such a small sample set one could expect much deeper analytical afford. Method descriptions partially missing and some data I found by luck in the supplements. In the cause of the review process I stopped marking down all individual specific comments. There was simply too much to correct and my time is limited.

General comments

The introduction should summarize the state of the art and introduce to the relevance of the topic. Unfortunately a larger part of the introduction (L51-70) contained technical information and methodological information. I recommend to go deeper into literature on soil management options of arable land and the connection between management of soil structure and water budget.

The study site is not characterized well. Climate data are missing at all and the distance between the two study sites is unclear. A map would help. No information on the type of management (experimental field trial or on farm research) is provided. Since this are calcareous soils, information about parent material would be helpful. How deep below soil surface starts the bedrock? Soil texture should be measured in replicates. The method must be described. Please show the data in the main manuscript from each sample. There must be a prove (correlation etc.) that there are no texture based differences on soil properties such as soil OC or CEC. It is recommended to show values from deeper soil layers (>30cm). Otherwise the effect of texture should be evaluated. There are also several uncertainties on fertilizer management: What form of OM amendments, how much, when in the crop rotation? What kind of cover crops? Please provided more details to the sampling design: Size of the fields, distance between the sampling points in a map.

Unsing an ANOVA approach for statistic comparison requires the assumption of normality. Further, the sample size of 3 is very low and likely not the suitable measure. I recommend using a simple T-test, depending on the distribution of the data.

The data set on microbial parameters should be incorporated in the main manuscript. Methods must descried properly. The same is true for the OC measurements. Have the carbonates be removed from the samples?

In the conclusion there something written with vegetable cover, that was not discussed before. I did not get this point. The author’s proclaimed the “optimized management” practices for the whole Mediterranean region. From this very limited data set at one sampling site it is not possible to scale up the management tools across the whole Mediterranean environment. Also the effects in the subsoil have not been taken into account.

I also highly recommend a professional language check. Many basic rules for preparing a scientific publication are ignored. For example: The manuscript is overloaded with double brackets, grammar errors or punctuation errors. Many paragraphs are not accessible, even after reading several times.

Specific comments:

L39 change eliminate to avoid. Further, cover cropping have nothing to do with soil tillage practices, examples for reduced soil tillage are e.g. mini tillage (0-10cm) , Cultivator application and everything that avoids to invert the soil of 0-30cm.

L 43 the annual soil water balance primarily depend on precipitation: I suggest optimisation of the infiltration and water storing capacity

L51-70 this belongs to the materials &method section. If you write a paper on the methods you could bring this here.

L78 managed

L86-88 the sentence is overloaded with brackets. Avoid double brackets and remove some them. Keep this in mind for the rest of the manuscript.  

L97-102 this is unclear. Is only the cereal straw removed from the fields? I never heard that straw of legumes and rapeseed is removed?

L 107 which form of OM amendments, how much nutrients and OC therein?

L245 - following. Use space between ± and the number. The same is true for >. Only between the numbers an % there should not be a space.

L235-238 no consistency Fig. Figure. The two paragraphs double.

L246 texture homogeneity was not measured.

L311 where does the vegetable cover comes from ?

I strongly support field research and the cropping system approach instead of individual practice comparison and believe in the extra value of long-term experiments.  Thus, I feel that this research will definitely contribute to the existing knowledge. Nevertheless, as the other reviewers also commented,  the manuscript needs improvements before being published.

I considered all the comments of the  other reviewers and will not repeat them as I mostly agree with both.  I will indeed stress though that when in a cropping system the term sustainability is included then all aspects should be considered (social economic and environmental).

The title would be more representative if it was something like “the effects of long-term conservation management on topsoil structure”.

In the introduction, a more thorough review of the effects of the specific management practices on soil quality or at least on the WRC and soil aggregates should be included, and specific scientific questions and hypotheses should be structured.

The section materials and methods should be written in a clearer way.

Starting from the description of the treatments where more details should be included, such as the frequency and type of organic amendment and cover crops rather than occasional use. Also the type of mineral fertilization the quantities and frequency. Possibly a table with the crop rotation history and amendments application would be useful. 

The soil's initial characteristics (for the variables that are available) will give valuable information on the effects. That is an extra value of the long term experiments and you should present it. 

  Focusing on the sampling procedures and especially the mixed subsample for the determination of the distribution of the aggregate, it is not clear how the required replication for the statistical analysis (at least 3 samples) happened as you indicate that “three sub-samples per sampling point, which were then mixed to obtain a composite sample)”. As it is written it is not clear if you ended up with one composite sample per treatment or with three samples one at each sampling point.

In L: 105 you mention “Organic fertilization was not used in any of the study treatments until the experiment year in which an organic amendment was applied to the soil without disturbing the surface in the OPM treatment.” What do you mean by experiment year?  Before you mentioned that in the OPM there is frequent application of organic amendments. Do you mean before the beginning of the experiment? Ie 18 years ago?   Rephrase the sentence. 

In the results as well as in Table 1 you should indicate where the differences were significant. Which post-hoc test did you perform?  In Figure 4, you should clearly mention what the error bars represent, you should include error bars in the in-between Magg fractions also to allow comparisons, and letters on top of each bar to indicate significant differences between the two treatments.

Focusing more on the aggregates the authors refer to the hierarchical aggregate order concept by Tisdall and Oades (1982). The wrongly present that the authors cited, mention that the magg are bonded together to form Magg.  What is actually mentioned in the majority of the cited papers (eg Oades, 1984; Six et al., 1999, 2004;) is what was revised by Oades (1984) and validated by Angers (1997) that magg are formed within the Magg and not before these. The authors should correct all this paragraph and explain their results accordingly.  

In the results and discussion section, the authors should interpret their results in terms of causes,  compared them with the existing literature in a more detailed way,  and give practical recommendations according to their results.

I hope that my recommendations along with those of the other reviewers will help you to improve the manuscript. 

Dear Authors,

I read with pleasure your MS entitled “Evaluation of a long-term optimized management strategy for the improvement of cultivated soils in rainfed cereal cropland based on water retention curves” by Aldaz-Lusarreta et al. The MS deals with the effect of an optimized agronomic protocol on water retention curve, pore size distribution (PSD) and aggregate stability. The Authors concluded that the soil under the optimized system reflected a better quality –or less degradation– compared to conventional management after 18 years of adoption.

The MS falls within the Journal’s scope and will interest Journal’s readers however I have some major and minor issues to draw to your attention.

• The structure of the abstract should be re-arranged by clearly dividing it into classical sections (introduction, M&M, results, conclusions). In particular, a few sentences regarding M&M should be added to introduce the reader to the work you did.
• What is the caution of applying organic amendments under no-till? Nitrate Directive and, the more recent NEC Directive claim for greater caution in applying N sources. How can you meet environmental criteria by broadcasting organic waste on the soil surface and not incorporating it? This would result in greater ammonia volatilization and a high risk of leaching. Consequently, also the nitrogen use efficiency would result very low without improving the soil structure due to the low amendments-soil particle mixing.
• The Authors used an indirect method (capillary method) to estimate the PSD however nowadays a lot of direct non-destructive methods are available for a direct assessment of PSD. Therefore, the limitations of your study as related to the adopted methods should be included and discussed in detail.
• The authors presented the water retention curves but only tested the statistical differences between some relevant points (e.g., at saturation). Contrarily, a direct statistical comparison between the curves might give more value to your study.
• LL85-86: please insert standard WRB soil classification
• A more in deep discussion of your data as related to other published studies is missing in particular in the PSD section. There is a lot of literature on how different agronomic managements impact PSD. Just for example:
  • Conservation Agriculture Had a Poor Impact on the Soil Porosity of Veneto Low-lying Plain Silty Soils after a 5-year Transition Period. Piccoli, I., Camarotto, C., Lazzaro, B., Furlan, L., Morari, F. Land Degradation and Development, 2017, 28(7), pp. 2039–2050.
  • Zero tillage has important consequences for soil pore architecture and hydraulic transport: A review. Wardak, D.L.R., Padia, F.N., de Heer, M.I., Sturrock, C.J., Mooney, S.J. Geoderma, 2022. 422,115927
• The conclusion section needs to be re-arranged by removing the summary-like part (LL301-316) and should go beyond the study results

This article is an experimental study on the effect of conservation agricultural practices. Thus, an optimal treatment (OPM) is compared to a conventional treatment with a 15 cm ploughing. From my point of view the strong points of this study are: 1) the choice of treatments with the analysis of the condition obtained after 18 years of direct seeding. The documentation of long-term effects is a very valuable contribution. 2) the use of a structural stability test that I find relevant for this type of treatment. Around these strong points the study brings clear results, namely significant effects on macroporosity and structural stability.

However, the study also suffers from weak points. The experimental design remains minimalist (6 samples 3 per treatment). It is not clear whether the samples were taken on one field or whether 3 plots were observed with one sampling point per field. In the latter case, the lack of replication is a problem. Indeed, it is very likely that different fields, even if managed according to the same strategy, probably have different short and long term cropping histories. For soil characterisation, we remain somewhat in the midstream. Indeed, the functional consequences can only be partially addressed. On the SWRC, the water storage capacity, which likely is one of the most interesting property, cannot be addressed, as the measurements at the wilting point are not reported. Macroporosity is of interest for infiltration. Hydraulic conductivity measurements at saturation and/or near saturation would have allowed to interpret the clear differences in porosity and their consequence on the water flows. Previous studies have shown that the absence of tillage leads to a restructuring of the pore space which could lead to a continuity of macropores that might favour infiltraton. The link between structural stability and erosion risk, as mentioned in the conclusion, is also an interesting point that could be further investigated. To what extent can the difference in structural stabilities, as observed, play on the erosion risk.

On the form the article could be improved.

1) The apriori statement that no tillage is optimal is questionable. The study should contribute to knowledge that could be used to support such an assertion.

2) The state of the art in the introduction is very succinct. There is a lot of existing work that deals with the impact of conservation agriculture on soil properties. Some elements are given in the analysis of the results. A more extensive state of the art would allow to better situate the results. The subject is already well studied, but it is still important to document new cases (as that of the presented study) due to the complexity of the subject. Such a state-of-the-art analysis could highlight the originality of results obtained in the study.

3) The text is not always easy to read and follow, especially in the methodological and results analysis sections.

Specific points

L105  : when organic fertilizer was applied in OPM?

Table 1 : Soil granulometry would be a very valuable to interpret the results. This cannot be replaced by the fractions obtained for the structural stability.

L140 : how the inflexion determined (second derivative = 0?).

Section 2.4 : as this method is the less common, it would interesting to introduce first the type of information that can be characterized and then give some key to understand the results. Can the stability properties be related to erosion risk?

L195-198 it is a bit confusing to highlight that below field capacity the soil water capacity is comparable between treatments. This would mean that the water availability of the water storage (below field capacity) would not be affected by the treatments. It would be useful to analyse the moisture variations from field capacity to the driest points (idealy , the wilting point) that may lead to significant differences

Table 2 and 3 : the moisture at inflexion point differed a lot between treatments and analytic SWRC curve. Can you comment this.

Section 3.3 : how the porosity spectrum established?

L266-268 : rephrase

L276-279 :  not clear

L280-283 : rephrase

L305-L308 a bit speculative without going further in the SWRC between Field capacity and the dry point the difference in water content is comparable

L319-321  : No data for infiltration. Results are over interpreted

L322-L327 : establish clearly the criteria that support the judgement. For instance, macroporosity can be associated to potentially good infiltration which is in favour to CM. For me there is a bias in favour to OPM that start from the introduction and goes toward the conclusion. (I am not against OPM but in evaluating agricultural systems we must stay as objective as possible).

In conclusion : in its present form the paper cannot be published. I suggest major revision including, if possible, more results (texture, infiltration, wilting points…) and/or a clear articulation between the state of art and the findings.