the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 23 Dec 2025
Two Decades of Conservation Agriculture Enhances Soil Structure, Carbon Sequestration, and Water Retention in Mediterranean Soils
Abstract. Conservation agriculture offers a pathway for enhancing soil health with climate co-benefits in Mediterranean agricultural systems. This study examined long-term impacts of combining no-till management with cover cropping over 20 years in California's Central Valley, providing rare insights into soil system equilibrium under sustained conservation management. We assessed soil physical, chemical, and structural properties comparing reduced tillage with cover crops (CTCC) to standard tillage without cover crops (STNC), employing density fractionation and spectroscopic analysis to understand carbon protection mechanisms. After two decades, conservation agriculture achieved dynamic equilibrium characterized by fundamental shifts in carbon stabilization pathways. Water-stable aggregate analysis revealed the most pronounced management effects, with CTCC exhibiting 136% greater stability than STNC, indicating substantial improvements in soil structural integrity. These structural enhancements corresponded with a reorganization of carbon protection mechanisms: CTCC disproportionately enriched the occluded light fraction (44.1% vs. 35.4% of total recovered carbon in STNC), demonstrating that physical protection within aggregates becomes a dominant carbon stabilization pathway under long-term conservation management. Mineral-associated organic carbon saturation analysis revealed that both management systems remained well below theoretical maximum capacity (11.5% vs. 7.4% saturation for CTCC and STNC, respectively), indicating substantial remaining potential for carbon sequestration even after reaching equilibrium. Physical property improvements under CTCC included 15% lower bulk density and 13% greater water retention at field capacity, though benefits were concentrated in the surface horizon. Our findings demonstrate that two decades of conservation agriculture fundamentally transforms soil functioning through aggregate-mediated physical protection, while creating substantial improvements in soil structural integrity and water retention capacity. This mechanism shift represents a new soil system equilibrium that maintains enhanced functionality and continued carbon sequestration potential in Mediterranean agricultural systems.
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RC1: 'Comment on egusphere-2025-6047', Anonymous Referee #1, 29 Jan 2026
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AC1: 'Reply on RC1', Teamrat Ghezzehei, 10 Apr 2026
Manuscript egusphere-2025-6047: Two Decades of Conservation Agriculture Enhances Soil Structure, Carbon Sequestration, and Water Retention in Mediterranean Soils
Alvarez-Sagrero, Berhe, Chacon, Mitchell, and Ghezzehei
General Response
We thank Reviewer 1 for the careful and constructive evaluation of our manuscript. We appreciate the recognition that the narrative is generally coherent, the writing easy to follow, and the data clearly presented. The three general comments, concerning the dynamic equilibrium framing, consistency in treatment presentation, and statistical approach, are well taken and will lead to substantive improvements. Below we address each general and specific comment in turn.
1. Dynamic Equilibrium Framing
Reviewer Comment: The authors argue that 20 years of conservation practices have led to the establishment of a new dynamic equilibrium. In my view, demonstrating a dynamic equilibrium typically requires time-series data showing stabilization of key variables… While this is a reasonable hypothesis, it remains unclear whether the system has reached equilibrium or is still in the process of approaching it… I would recommend softening the language.
Response: We agree that our single time-point comparison cannot establish whether key variables have stabilized, and that our strongest claims overstate what the data can support. We will revise the most assertive language, particularly in the Abstract and Conclusions, to present equilibrium as a plausible interpretation framed by the literature rather than a demonstrated outcome. For example, we will replace “conservation agriculture achieved dynamic equilibrium” with language such as “after two decades of implementation, conservation agriculture produced soil conditions consistent with the approach toward a management-induced steady state described for systems managed >15 years (Caruso et al., 2018; West and Post, 2002).”
We will retain a more cautious discussion of equilibrium as a possible interpretive framework in the Discussion, since the literature on long-term conservation systems provides strong theoretical support for this trajectory. However, we will soften the framing where it reads as a confirmed finding and reduce the prominence of Tian et al. (2024), whose 10-year duration did not directly observe the >15-year mature phase we invoke. We will broaden the supporting literature and present the temporal interpretation more cautiously as a working framework.
Proposed Revision (Discussion, lines 443–454): “Our carbon accumulation patterns are consistent with the trajectory toward dynamic equilibrium described for conservation agriculture systems managed for 15–20 years (Caruso et al., 2018; West and Post, 2002). However, our cross-sectional design does not permit direct confirmation of equilibrium status, and the evolving management trajectory at this site (Section 2.2) means the system may still be on a trajectory of change. Additional temporal data would be valuable for resolving this question.”
2. Consistency in Treatment Presentation
Reviewer Comment: Figure 1 presents the results on aggregate stability for all four treatments. For consistency, the authors should either include the intermediate treatments throughout the paper or remove them from Figure 1.
Response: Figure 1 is intentionally designed to include all four treatments, and we consider it essential to the main text. The decision to focus subsequent analyses on CTCC and STNC was empirically motivated by prior work at this site (Araya et al., 2022), which tested all four treatments at 0–5 and 20–25 cm depths and found significant hydrological differences only between the two management extremes. Figure 1 provides independent corroboration of this pattern: aggregate stability data confirm that the intermediate treatments (CTNC and STCC) show limited differentiation from STNC, particularly in the 4–8 mm size class (Tukey HSD: CTNC vs. STNC, p = 0.112; STCC vs. STNC, p = 0.087). This figure gives the reader the empirical basis for the endmember analytical focus adopted throughout the rest of the paper.
We will add a brief statement in the Results section clarifying this rationale and citing Araya et al. (2022).
3. Statistical Tests and Block Structure
Reviewer Comment: The manuscript reports the use of Welch’s t-tests and Mann-Whitney U tests (Section 2.11). These tests do not account for block effects or the paired structure inherent in a randomized complete block design. A paired t-test, or a linear mixed model including block as a random factor would be more appropriate.
Response: We agree that accounting for the block structure of the experimental design will strengthen the statistical analysis. The CASI experiment employs a randomized complete block design with eight blocks arranged along a clay content gradient. For the two-treatment comparisons that constitute the bulk of the paper (CTCC vs. STNC, n = 7 paired blocks for soil cores, n = 6 paired blocks for density fractionation), we will adopt paired tests (paired t-tests where distributional assumptions are met, and paired Wilcoxon signed-rank tests where they are not) which directly honor the block structure. For the four-treatment aggregate stability comparison (Figure 1), we will use a randomized block ANOVA with Games-Howell post-hoc tests to accommodate unequal variances.
Block information is already tracked in our data, so this reanalysis is straightforward to implement. Given the large effect sizes observed for primary variables (e.g., 136% difference in aggregate stability, approximately 100% difference in surface carbon stocks), we anticipate that accounting for block structure will provide a more appropriate and robust assessment of treatment effects.
All p-values, significance indicators, and figure caption test references will be updated accordingly. The revised Section 2.11 will describe the updated statistical framework.
Proposed Revision (Section 2.11): “For two-treatment comparisons under the randomized complete block design, paired t-tests (pairing by block) were used where normality and variance assumptions were satisfied; paired Wilcoxon signed-rank tests were applied otherwise. For multi-treatment comparisons (Figure 1), randomized block ANOVA was followed by Games-Howell post-hoc tests to accommodate unequal variances. Statistical significance was denoted at p < 0.05 (*), p < 0.01 (**), and p < 0.001 (***).”
Specific Comments
4. Introduction Wordiness (Lines 75–86)
Reviewer Comment: Parts of the Introduction are somewhat wordy and could be streamlined. For example, the paragraph describing advances in soil analytical techniques (lines 75–86) appears redundant, as the methods applied in this study are largely standard and well established.
Response: Agreed. We will substantially condense this paragraph, retaining only the information necessary to motivate our specific analytical approach without overstating methodological novelty. The Introduction will be streamlined throughout.
5. Variable Sample Sizes Across Figures
Reviewer Comment: Sample sizes vary among analyses, for example eight replicates in Figure 1, seven for carbon stocks in Figure 5, and six for carbon fractions in Figure 7. Please explain the reasons for these differences, whether any samples were excluded, and the criteria used for exclusion.
Response: Sample size variation reflects different sampling strategies and the availability of material from specific blocks. Aggregate stability (Figure 1, n = 8 per treatment) used bulk samples from all eight replicate blocks. Soil core analyses (Figure 5, n = 7) had one replicate excluded due to sampling or processing issues. Density fractionation (Figure 7, n = 6) was performed on bulk samples from six of the eight blocks; blocks 7 and 8 were not sampled for this analysis. All six sampled blocks passed the ±10% mass recovery criterion described in Section 2.10.
We will add a paragraph to the Methods documenting the sample sizes for each analysis and the specific blocks included. We will also report mass and carbon recoveries for the density fractionation procedure (see also our response to Reviewer 2, Comment 14), including a sample-level table showing bulk carbon content, mass recovery, and apparent carbon recovery for each sample.
6. Figure Citation Error (Line 399)
Reviewer Comment: The figure citation here should refer to Figure 7.
Response: Thank you. We will correct this.
7. Additive Effects Claim (Line 423)
Reviewer Comment: Claims of additive effects require explicit comparison with tillage-only and cover-crop-only treatments. Without these comparisons, the interpretation remains speculative.
Response: We acknowledge this limitation. The synergistic interpretation is directly supported by the aggregate stability data (Figure 1), where all four treatments were compared and CTCC significantly exceeded both single-factor treatments. However, we cannot extend this interpretation to other variables where only the endmember treatments were analyzed. We will revise line 423 accordingly: “The aggregate stability data suggest synergistic rather than purely additive effects of combining reduced tillage with cover cropping (Figure 1), though this interpretation cannot be extended to variables where intermediate treatments were not directly compared.”
8. Equilibrium Language (Lines 443–454)
Reviewer Comment: Confirmation of a mature or equilibrium phase requires temporal data. Without time-series evidence, conclusions about reaching a stable phase should be softened.
Response: Agreed. This will be addressed as part of the reframing described in our response to General Comment 1.
9. Carbon Saturation Gap (Line 470)
Reviewer Comment: The large carbon saturation gap discussed here does not appear to represent a realistic or actionable target for conservation efforts in this system and should be framed more cautiously.
Response: We agree. The theoretical maximum from the Georgiou et al. (2022) framework represents an upper mineralogical bound that is not achievable under the environmental constraints of this Mediterranean system (low precipitation, seasonal aridity, limited carbon inputs during dry months). The system may have approached a management-induced steady state that is far below mineralogical capacity precisely because these environmental constraints, rather than mineral surface availability, limit carbon accumulation. We will revise this section to frame the saturation gap as indicating that mineral surfaces are not the primary constraint on carbon storage, rather than as unrealized sequestration potential. We will also propagate the uncertainty inherent in the Georgiou et al. framework (±9 mg C g⁻¹ mineral) through our calculations (see also our response to Reviewer 2, Comment 11).
10. Section 4.6 Wordiness
Reviewer Comment: The methodological insights are a bit wordy, given that these protocols are all standardized (line 556).
Response: Agreed. We will condense Section 4.6, focusing on the key finding that depth-stratified sampling is essential for detecting conservation agriculture effects and removing extended discussion of standardized protocols.
11. Streamlining the Conclusions
Reviewer Comment: Section 5 can be streamlined, in my opinion.
Response: Agreed. We will consolidate the Conclusions into a single cohesive section, removing the current subsection structure and focusing on principal findings and their direct implications.
Summary of Proposed Revisions
Global: Soften the strongest equilibrium assertions while retaining the interpretive framework; broaden literature base beyond Tian et al. (2024)
Section 2.11: Reanalyze with paired tests (pairing by block); randomized block ANOVA for Figure 1; add Games-Howell test description; update all figure caption test references
Methods: Document sample sizes and block coverage for each analysis; report mass and carbon recoveries for density fractionation
Introduction: Streamline, particularly lines 75–86
Results/Figures: Update all p-values and significance annotations; correct figure citation at line 399; add statement justifying the endmember focus with reference to Araya et al. (2022) and Figure 1
Discussion: Soften equilibrium claims; qualify additive effects interpretation; reframe carbon saturation gap as environmental constraint rather than unrealized potential; condense Section 4.6
Conclusions: Streamline into a single section
We believe these revisions will address the reviewer’s concerns while preserving the core contributions of the study. We look forward to the opportunity to submit a revised manuscript.
Citation: https://doi.org/10.5194/egusphere-2025-6047-AC1
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AC1: 'Reply on RC1', Teamrat Ghezzehei, 10 Apr 2026
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RC2: 'Comment on egusphere-2025-6047', Anonymous Referee #2, 17 Feb 2026
This manuscript will be a valuable contribution to our understanding of long-term conservation agriculture impacts in Mediterranean agricultural systems. The multi-method analytical approach of combining density fractionation, FTIR spectroscopy, aggregate stability, and comprehensive physical characterization is well-suited to the research questions. The figures are visually consistent and well-constructed, and the paper is engaging to read. The core finding, that sustained conservation management reorganizes carbon protection mechanisms toward aggregate-mediated physical protection while improving soil structural and hydraulic properties, is well-motivated and contributes meaningfully to ongoing discussions about carbon permanence and sequestration potential in dryland agricultural systems.
My principal comments are related to the dynamic equilibrium framing, the reporting of statistics, and management. I have listed general comments followed by specific comments below.
General comments:
The framing of the results as evidence that the soil system has reached "dynamic equilibrium" after 20 years is not supported by the study design. Demonstrating equilibrium requires temporal data showing that carbon stocks have stabilized, whereas this study provides a single time-point comparison after 20 years of divergent management, which is valuable on its own terms but cannot establish whether stocks are still changing. I recommend the authors reframe this language throughout, using the equilibrium concept as theoretical context drawn from the literature rather than a demonstrated outcome of this study. Related to this, the discussion leans heavily on Tian et al. (2024) as a basis for the temporal phases of carbon protection mechanisms. Although this reference is useful, it pertains to a different climate, soil type, and crop rotations, and it is also just one study. More significantly, citing it as the basis for the 0-5, 5-15, and 15+ year phase framework is problematic, because Tian et al. (2024) was a 10-year study, and so did not observe the mature phase beyond 15 years that the authors use to interpret the results. I recommend either citing literature that documents this, or being more cautious in how the temporal progression is framed.Relatedly, the discussion would benefit from addressing potential disconnects between the equilibrium framing and MAOC saturation. The authors assert that the system has reached management equilibrium and that much unsaturated mineral capacity remains. These are not mutually exclusive, but it's unclear how additional carbon will be sequestered to fill this capacity if management-related carbon sequestration has plateaued.
The characterization of the conservation treatment as a 20-year no-till experiment warrants more careful handling. As described in section 2.2, the no-till system permitted shallow cultivation for tomato crops from 1999-2011, with true no-till only achieved in 2012, meaning that for roughly the first 13 of the 20 study years, the system was more accurately described as reduced tillage than no-till. The paper's framing implies a consistency of management that is not supported by the methods. This has bearing on the equilibrium claim; if true no-till conditions were established relatively recently within the study period, the system could still be responding to that transition rather than having stabilized under consistent management. The authors should address this trajectory more explicitly, both in how they describe the treatment throughout the manuscript and in how they interpret the maturity of the soil system response.
Specific comments:
Throughout the manuscript, most results are presented as boxplots, which display medians and interquartile ranges. However, parametric tests comparing means (ANOVA, Welch's t-test) are reported for several variables. These are incongruent: where parametric tests are used, means with standard error bars would be the more appropriate display, and would also be more consistent with the error bar descriptions in several figure captions. The authors should either reconcile the figure types with the tests applied, or justify the mixed approach explicitly.
The Games-Howell post-hoc test appears in Figures 7 and 11 but is not mentioned anywhere in section 2.11. Please add it to the statistical methods description.
Figure 4 caption refers to a Wilcox test while the methods section describes Welch's t-test for two-group comparisons. Please reconcile.
The hydraulic conductivity results show a reversal between depths, with CTCC being higher at 0-5 cm and lower at 5-10 cm relative to STNC, that receives little discussion despite potentially meaningful implications for subsurface drainage and water redistribution. A brief interpretation would be useful.
The carbon retention efficiency estimate (19% of cover crop inputs retained) is a useful calculation but the denominator relies on estimated rather than directly measured cover crop biomass inputs over 20 years. This assumption should be stated explicitly and its uncertainty acknowledged.
Figure 4 caption cites a Wilcox test while the methods section describes Welch's t-test for two-group comparisons. Please reconcile.
The authors report MAOC saturation as point estimates but do not propagate the uncertainty inherent in the Georgiou et al. (2022) framework (±9 mg C g⁻¹ mineral) through their calculations. Given that this uncertainty represents roughly 10% of the central estimate, the saturation percentages carry uncertainty that could be reported. The authors' conclusion that both treatments remain well below theoretical maximum is likely robust to this, but reporting the propagated uncertainty would strengthen their conclusions.
Figure 8 presents proportional carbon and nitrogen distribution as stacked bars with no measure of variability, yet statistical comparisons between treatments are reported in the text for these proportions (section 3.5.3, p = 0.01 and p = 0.003). A reader has no way to visually assess the variability underlying those comparisons from the figure as presented. Error bars or an alternative figure type that conveys distributional information should be added.
Throughout the manuscript, significant figures are applied inconsistently. For example, aggregate stability is reported as 46.85 ± 15.22% alongside p-values carried to many decimal places, while other values are rounded to whole numbers. I recommend standardizing to reflect the actual precision of the measurements, following the conventions used elsewhere in this journal.
Citation: https://doi.org/10.5194/egusphere-2025-6047-RC2 -
AC2: 'Reply on RC2', Teamrat Ghezzehei, 10 Apr 2026
Manuscript egusphere-2025-6047: Two Decades of Conservation Agriculture Enhances Soil Structure, Carbon Sequestration, and Water Retention in Mediterranean Soils
Alvarez-Sagrero, Berhe, Chacon, Mitchell, and Ghezzehei
General Response
We thank Reviewer 2 for the thorough and insightful evaluation of our manuscript. We are grateful for the recognition that the multi-method analytical approach is well-suited to the research questions, that the figures are well-constructed, and that the core finding regarding reorganization of carbon protection mechanisms contributes meaningfully to ongoing discussions about carbon permanence. The principal comments regarding the dynamic equilibrium framing, treatment characterization, and statistical reporting are incisive and will substantially strengthen the manuscript. We address each point below.
1. Dynamic Equilibrium Framing
Reviewer Comment: The framing of the results as evidence that the soil system has reached “dynamic equilibrium” after 20 years is not supported by the study design. Demonstrating equilibrium requires temporal data showing that carbon stocks have stabilized, whereas this study provides a single time-point comparison… I recommend the authors reframe this language throughout, using the equilibrium concept as theoretical context drawn from the literature rather than a demonstrated outcome of this study.
Response: We agree that the strongest equilibrium assertions in the manuscript overstate what a cross-sectional comparison can support. We will revise the Abstract and Conclusions to present equilibrium as a plausible interpretation rather than a demonstrated outcome; for example, replacing “conservation agriculture achieved dynamic equilibrium” with “conservation agriculture produced soil conditions consistent with the approach toward a management-induced steady state described for systems managed >15 years (Caruso et al., 2018; West and Post, 2002).”
We will retain the equilibrium concept as an interpretive framework in the Discussion, since our 20-year dataset and the magnitude of the observed effects (136% aggregate stability improvement, ~100% surface carbon increase) are consistent with the literature on mature conservation systems. However, the framing will acknowledge the limitations of our design and note that the evolving management trajectory at this site (see Comment 4) provides an additional reason for interpretive caution. This reframing aligns with Reviewer 1’s General Comment 1.
2. Tian et al. (2024) Temporal Phase Framework
Reviewer Comment: Citing Tian et al. (2024) as the basis for the 0–5, 5–15, and 15+ year phase framework is problematic, because Tian et al. (2024) was a 10-year study, and so did not observe the mature phase beyond 15 years… I recommend either citing literature that documents this, or being more cautious in how the temporal progression is framed.
Response: This is an important point. We will: (a) explicitly acknowledge that Tian et al. (2024) did not directly observe the >15-year phase; (b) broaden the literature base with additional long-term studies documenting system behavior beyond 15 years (e.g., Caruso et al., 2018; West and Post, 2002, who reported declining carbon sequestration rates approaching equilibrium within 15–20 years across diverse systems); and (c) present the temporal phase interpretation as a working framework rather than an established trajectory, noting differences in climate, soil type, and cropping system between our site and the referenced studies
3. Disconnect Between Equilibrium Framing and MAOC Saturation
Reviewer Comment:The authors assert that the system has reached management equilibrium and that much unsaturated mineral capacity remains. These are not mutually exclusive, but it’s unclear how additional carbon will be sequestered to fill this capacity if management-related carbon sequestration has plateaued.
Response: This is a perceptive observation that identifies a logical tension we had not adequately addressed. We will add a paragraph to the Discussion making the following argument: the system may have approached a management-induced steady state that is far below mineralogical capacity precisely because environmental constraints, low precipitation, seasonal aridity, and limited carbon inputs during dry months, rather than mineral surface availability, limit carbon accumulation. The theoretical maximum from Georgiou et al. (2022) represents an upper mineralogical bound that is not achievable under these conditions. The saturation gap should therefore be interpreted as evidence that mineral surfaces are not the bottleneck constraining carbon storage in this system, rather than as unrealized potential under current management. Closing the remaining gap would likely require fundamentally different interventions (e.g., organic amendments, irrigation changes, deeper-rooted perennials) rather than continuation of the current conservation management
4. Treatment Characterization: Reduced Tillage vs. No-Till
Reviewer Comment: The characterization of the conservation treatment as a 20-year no-till experiment warrants more careful handling. As described in section 2.2, the no-till system permitted shallow cultivation for tomato crops from 1999–2011, with true no-till only achieved in 2012… The paper’s framing implies a consistency of management that is not supported by the methods… The authors should address this trajectory more explicitly.
Response: We agree that the treatment description requires more careful handling. The manuscript already uses the abbreviation CTCC (Conservation Tillage with Cover Crops), which accurately reflects the reduced-tillage character of the management. We will correct the few places where “no-till” is used casually in the Introduction and Discussion to be consistent with this terminology. More importantly, we will add a paragraph to the Discussion explicitly describing the management trajectory, reduced tillage with shallow cultivation for tomato crops (1999–2011) transitioning to true zero-tillage (2012–present), and acknowledging that true no-till conditions were established only approximately 7 years before sampling.
This management trajectory has two important implications for interpretation: (1) it directly supports our revised framing that equilibrium is a plausible trajectory rather than a confirmed outcome, since the system may still be responding to the intensification of disturbance reduction; and (2) it is representative of how conservation agriculture adoption typically occurs in practice (through incremental intensification rather than abrupt transitions) meaning our results capture a realistic adoption scenario.
Proposed Revision (Discussion): “The CT system permitted shallow cultivation for tomato crops from 1999–2011, with true zero-tillage achieved only in 2012 (Section 2.2). The system thus experienced approximately 13 years of reduced tillage followed by 7 years of true no-till before sampling. This management trajectory means our observations likely capture a system on a continuing trajectory of improvement rather than one fully equilibrated under consistent management. This progressive adoption pathway is, however, representative of real-world conservation agriculture implementation.”
5. Boxplots vs. Parametric Tests
Reviewer Comment: Throughout the manuscript, most results are presented as boxplots, which display medians and interquartile ranges. However, parametric tests comparing means are reported… The authors should either reconcile the figure types with the tests applied, or justify the mixed approach explicitly.
Response: We will justify the mixed approach. We retain boxplots with individual data points (jitter overlay) throughout because they transparently display data distributions, which we consider essential given our sample sizes (n = 6–7). At these sample sizes, boxplots provide the reader with a more honest picture of the data than bar plots showing only means and standard errors. Statistical inferences are based on paired tests (see Comment 8), and the specific test applied is reported in each figure caption. We will add a brief justification in Section 2.11 explaining this choice.
6. Games-Howell Post-hoc Test
Reviewer Comment: The Games-Howell post-hoc test appears in Figures 7 and 11 but is not mentioned anywhere in section 2.11. Please add it to the statistical methods description.
Response: We will add the Games-Howell test to Section 2.11.
7. Figure 4 Caption: Wilcox vs. Welch’s t-test
Reviewer Comment: Figure 4 caption refers to a Wilcox test while the methods section describes Welch’s t-test for two-group comparisons. Please reconcile.
Response: We will reconcile all figure captions with the statistical tests actually applied following the reanalysis with paired tests (see Comment 8).
8. Statistical Tests and Block Structure
Reviewer Comment: These tests do not account for block effects or the paired structure inherent in a randomized complete block design… A paired t-test, or a linear mixed model including block as a random factor would be more appropriate.
Response: Agreed. The CASI experiment uses eight blocks arranged along a clay content gradient. For the two-treatment comparisons that constitute the bulk of the paper (CTCC vs. STNC), block pairing is preserved: n = 7 paired blocks for soil core analyses, n = 6 paired blocks for density fractionation (six of the eight blocks were sampled for this analysis; see Comment 14 in Reviewer 1’s response for details on sample coverage). We will reanalyze using paired t-tests where distributional assumptions are met, and paired Wilcoxon signed-rank tests otherwise. For the four-treatment aggregate stability comparison (Figure 1), we will use a randomized block ANOVA with Games-Howell post-hoc tests. All p-values, significance annotations, and figure caption test references will be updated. This addresses the same concern raised by Reviewer 1 (General Comment 3).
9. Hydraulic Conductivity Depth Reversal
Reviewer Comment: The hydraulic conductivity results show a reversal between depths, with CTCC being higher at 0–5 cm and lower at 5–10 cm relative to STNC, that receives little discussion despite potentially meaningful implications for subsurface drainage and water redistribution.
Response: We will add a brief interpretation to the Discussion. The higher conductivity of CTCC at 0–5 cm likely reflects enhanced macroporosity from biological activity and root channels preserved by the absence of tillage. The reversal at 5–10 cm may reflect the absence of tillage-induced macropores that transiently increase conductivity under standard management, while the conservation system retains its undisturbed pore architecture. We note, however, that conductivity differences were not statistically significant at either depth due to high spatial variability (0–5 cm: p = 0.074; 5–10 cm: p = 0.284), and the interpretation should be understood as directional rather than conclusive.
10. Carbon Retention Efficiency Uncertainty
Reviewer Comment: The carbon retention efficiency estimate (19% of cover crop inputs retained) is a useful calculation but the denominator relies on estimated rather than directly measured cover crop biomass inputs over 20 years. This assumption should be stated explicitly and its uncertainty acknowledged.
Response: Agreed. We will explicitly state that the 19% retention estimate is based on cumulative estimated cover crop biomass inputs derived from periodic site-specific measurements extrapolated across the 20-year period, and acknowledge the uncertainty arising from year-to-year variation in cover crop productivity, composition, and decomposition. We will report the plausible range given known biomass variability at this site.
11. MAOC Saturation Uncertainty Propagation
Reviewer Comment: The authors report MAOC saturation as point estimates but do not propagate the uncertainty inherent in the Georgiou et al. (2022) framework (±9 mg C g⁻¹ mineral) through their calculations… reporting the propagated uncertainty would strengthen their conclusions.
Response: We will propagate the ±9 mg C g⁻¹ mineral uncertainty through our saturation calculations using the per-sample clay + silt data and report the resulting confidence intervals on saturation percentages. The conclusion that both treatments remain well below theoretical capacity is robust to this uncertainty, but reporting propagated intervals will provide more transparent assessment.
12. MAOC Saturation Hypothesis (Line 93)
Reviewer Comment: It is unclear why the authors hypothesize that the system is approaching a saturation limit for mineral-associated organic carbon, given the fine soil texture, relatively low carbon inputs, and dry climate.
Response: The reviewer is correct that our results showed the system is far from saturation, making the original hypothesis misleading. We will revise the hypothesis to state that we aimed to assess the degree of mineral-associated carbon saturation under long-term conservation management, without presupposing proximity to saturation.
Proposed Revision (line 93): “We hypothesized that long-term conservation management enhances aggregate-mediated physical protection of soil organic matter. We further assessed the degree of mineral-associated carbon saturation to evaluate whether mineral surface availability represents a primary constraint on carbon storage in this system.”
13. C=O Functional Group Assignment (Lines 267–268)
Reviewer Comment: The assignment of the C=O functional group as microbially derived organic carbon appears overly simplistic. There is evidence that other functional groups, such as amides and aromatics, may also contribute to signals in this range (Parikh et al. 2014), and the terminology should be revised or qualified.
Response: We agree. The 1660–1580 cm⁻¹ region encompasses C=O stretching of carbonyl groups but can also include contributions from amide I bands and aromatic C=C vibrations. We will revise the terminology to “processed organic matter” or “microbially-associated organic matter” and add a qualifying citation to Parikh et al. (2014).
14. Mass and Carbon Recoveries (Section 2.8)
Reviewer Comment: Please report mass and carbon recoveries for the fractionation procedure. This information is important for evaluating data quality and consistency.
Response: We will report a sample-level table including bulk carbon content, mass recovery, and apparent carbon recovery for all density fractionation samples. Mass recoveries were consistently within ±4% across both treatments (CTCC: 99.7 ± 3.1%; STNC: 100.5 ± 4.2%), confirming procedural integrity. Apparent carbon recovery showed greater variability (CTCC: 89.2 ± 6.4%; STNC: 81.8 ± 7.7%). This apparent carbon discrepancy reflects both dissolved organic carbon lost during SPT washing steps and heterogeneity in carbon content between the subsample used for bulk elemental analysis and the separate subsample used for fractionation. Within STNC, there is an apparent inverse relationship between bulk carbon content and carbon recovery. The worst recovery corresponds to the Block 5 (plot 19), which also had substantially higher C concentration than the mean.
Sample
Treatment
Block
Bulk C (%)
Mass recov. (%)
C recov. (%)
CTCC18-03
CTCC
1
2.36
98.2
97.2
CTCC18-08
CTCC
2
1.11
103.7
86.1
CTCC18-09
CTCC
3
1.52
96.1
88.0
CTCC18-15
CTCC
4
1.41
103.0
86.6
CTCC18-18
CTCC
5
2.03
100.0
81.0
CTCC18-24
CTCC
6
1.36
97.1
96.5
STNC18-02
STNC
1
1.16
98.1
85.2
STNC18-06
STNC
2
0.84
103.4
85.1
STNC18-11
STNC
3
0.85
104.4
87.0
STNC18-14
STNC
4
0.76
104.9
85.6
STNC18-19
STNC
5
1.55
96.2
66.4
STNC18-22
STNC
6
1.13
96.0
81.5
Samples from blocks 7 and 8 were not processed for density fractionation. All samples passed the ±10% mass recovery criterion described in Section 2.10.
15. Figure 2 Caption Typo
Reviewer Comment: There appears to be a typo indicated by two question marks.
Response: Thank you. We will correct this.
16. Comparative Language Without Statistical Support (Lines 348, 352)
Reviewer Comment: In several places, the manuscript uses comparative language such as “higher” or “lower” even when differences are not statistically significant. I recommend avoiding such terminology unless supported by statistical tests.
Response: Agreed. We will revise the Results to use neutral language (e.g., “did not differ significantly between treatments”) for all non-significant comparisons. Directional language will be reserved for statistically significant differences.
17. Figure 8: Variability in Stacked Bars
Reviewer Comment: Figure 8 presents proportional carbon and nitrogen distribution as stacked bars with no measure of variability, yet statistical comparisons between treatments are reported in the text… Error bars or an alternative figure type that conveys distributional information should be added.
Response: Agreed. We will revise Figure 8 to a grouped bar or boxplot format that displays the variability underlying the reported comparisons, with individual data points shown.
18. Significant Figures Consistency
Reviewer Comment: Throughout the manuscript, significant figures are applied inconsistently… I recommend standardizing to reflect the actual precision of the measurements, following the conventions used elsewhere in this journal.
Response: Agreed. We will standardize significant figures throughout, reporting means and standard errors to consistent decimal places within each variable, and p-values uniformly (three decimal places or p < 0.001).
Summary of Proposed Revisions
- Global: Soften the strongest equilibrium assertions while retaining the interpretive framework; correct casual use of “no-till” to match CTCC terminology; standardize significant figures; remove unsupported comparative language
- Abstract: Soften equilibrium claims
- Introduction: Revise MAOC saturation hypothesis (line 93); streamline analytical techniques paragraph
- Section 2.2: Add management trajectory description to the Discussion rather than revising the Methods, which already describe the history accurately
- Section 2.8: Report sample-level mass and carbon recoveries for density fractionation
- Section 2.11: Implement paired tests with block pairing; randomized block ANOVA for Figure 1; add Games-Howell description; justify boxplot retention; reconcile all test references in captions
- Results/Figures: Update all statistical annotations; revise Figure 8 to show variability; correct Figure 2 typo and line 399 citation
- Discussion: Add management trajectory paragraph; address equilibrium–MAOC saturation disconnect; broaden literature base beyond Tian et al. (2024); briefly interpret hydraulic conductivity reversal; acknowledge carbon retention efficiency uncertainty; propagate MAOC uncertainty; qualify C=O spectral assignment
- Conclusions: Streamline (also raised by Reviewer 1)
We believe these revisions will substantially strengthen the manuscript while preserving its core contributions. We look forward to the opportunity to submit a revised manuscript.
Citation: https://doi.org/10.5194/egusphere-2025-6047-AC2
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AC2: 'Reply on RC2', Teamrat Ghezzehei, 10 Apr 2026
Peer review completion
Interactive discussion
Status: closed
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RC1: 'Comment on egusphere-2025-6047', Anonymous Referee #1, 29 Jan 2026
Alvarez-Sagrero et al. examine the combined effects of reduced tillage and cover cropping on soil structure, carbon storage, and organic matter composition. Overall, I do not have major concerns with the study. The narrative is generally coherent, the writing is easy to follow, and the data are clearly presented. Some sections of the Introduction and Discussion are somewhat wordy and could be streamlined, and a few inconsistencies in statistical treatment should be addressed. I provide general comments on the framing and analysis below, followed by additional specific comments.
My first general comment concerns the repeated use of the term “dynamic equilibrium” in the Abstract and Discussion (e.g., lines 6, 18, and 448). The authors argue that 20 years of conservation practices have led to the establishment of a new dynamic equilibrium. In my view, demonstrating a dynamic equilibrium typically requires time-series data showing stabilization of key variables, as was shown in Caruso et al. 2018 and Tian et al. 2024, both were cited by the authors. In the present manuscript, this inference is largely based on comparisons to other systems and on the assumption that 15 to 20 years is sufficient to reach equilibrium (line 448). While this is a reasonable hypothesis, it remains unclear whether the system has reached equilibrium or is still in the process of approaching it. This is not a critical flaw, but I would recommend softening the language. For example, the authors could emphasize that conservation agriculture can lead to such an equilibrium and that the observed differences are meaningful, while noting that additional temporal data, including future measurements or archived soil analyses, would be needed to confirm equilibrium status.
My second general comment relates to consistency in the statistical approach. In the Methods, the authors state that their primary comparison focuses on combined reduced tillage and cover cropping versus conventional tillage without cover crops, with intermediate treatments excluded due to limited effects (lines 176-180). However, Figure 1 presents the results on aggregate stability for all four treatments. For consistency, the authors should either include the intermediate treatments throughout the paper or remove them from Figure 1.
Relatedly, the statistical tests used to assess treatment effects deserve reconsideration. The manuscript reports the use of Welch’s t tests and Mann-Whitney U tests (Section 2.11). These tests do not account for block effects or the paired structure inherent in a randomized complete block design (line 106). A paired t-test, or a linear mixed model including block as a random factor would be more appropriate and would strengthen the statistical rigor of the study.
Specific comments:
Introduction: Parts of the Introduction are somewhat wordy and could be streamlined. For example, the paragraph describing advances in soil analytical techniques (lines 75-86) appears redundant, as the methods applied in this study are largely standard and well established.
Line 93: It is unclear why the authors hypothesize that the system is approaching a saturation limit for mineral-associated organic carbon, given the fine soil texture, relatively low carbon inputs, and dry climate. Later results indicate that observed carbon stocks are far below theoretical saturation levels. It is debatable whether these gaps represent realistic or achievable carbon sequestration potential in this system, and this point should be discussed more cautiously.
Lines 267-268: The assignment of the C=O functional group as microbially derived organic carbon appears overly simplistic. There is evidence that other functional groups, such as amides and aromatics, may also contribute to signals in this range (Parikh et al. 2014), and the terminology should be revised or qualified.
Section 2.8: Please report mass and carbon recoveries for the fractionation procedure. This information is important for evaluating data quality and consistency.
Figure 2 caption: There appears to be a typo indicated by two question marks.
Results, including lines 348 and 352: In several places, the manuscript uses comparative language such as “higher” or “lower” even when differences are not statistically significant. I recommend avoiding such terminology unless supported by statistical tests.
Sample sizes across figures: Sample sizes vary among analyses, for example eight replicates in Figure 1, seven for carbon stocks in Figure 5, and six for carbon fractions in Figure 7. Please explain the reasons for these differences, whether any samples were excluded, and the criteria used for exclusion.
Line 399: The figure citation here should refer to Figure 7.
Line 423: Claims of additive effects require explicit comparison with tillage-only and cover-crop-only treatments. Without these comparisons, the interpretation remains speculative.
Lines 443-454: As noted earlier, confirmation of a mature or equilibrium phase requires temporal data. Without time-series evidence, conclusions about reaching a stable phase should be softened.
Line 470: The large carbon saturation gap discussed here does not appear to represent a realistic or actionable target for conservation efforts in this system and should be framed more cautiously.
Section 4.6: The methodological insights are a bit wordy, given that these protocols areall standardized (line 556).
Section 5 can be streamlined, in my opinion.
Citation: https://doi.org/10.5194/egusphere-2025-6047-RC1 -
AC1: 'Reply on RC1', Teamrat Ghezzehei, 10 Apr 2026
Manuscript egusphere-2025-6047: Two Decades of Conservation Agriculture Enhances Soil Structure, Carbon Sequestration, and Water Retention in Mediterranean Soils
Alvarez-Sagrero, Berhe, Chacon, Mitchell, and Ghezzehei
General Response
We thank Reviewer 1 for the careful and constructive evaluation of our manuscript. We appreciate the recognition that the narrative is generally coherent, the writing easy to follow, and the data clearly presented. The three general comments, concerning the dynamic equilibrium framing, consistency in treatment presentation, and statistical approach, are well taken and will lead to substantive improvements. Below we address each general and specific comment in turn.
1. Dynamic Equilibrium Framing
Reviewer Comment: The authors argue that 20 years of conservation practices have led to the establishment of a new dynamic equilibrium. In my view, demonstrating a dynamic equilibrium typically requires time-series data showing stabilization of key variables… While this is a reasonable hypothesis, it remains unclear whether the system has reached equilibrium or is still in the process of approaching it… I would recommend softening the language.
Response: We agree that our single time-point comparison cannot establish whether key variables have stabilized, and that our strongest claims overstate what the data can support. We will revise the most assertive language, particularly in the Abstract and Conclusions, to present equilibrium as a plausible interpretation framed by the literature rather than a demonstrated outcome. For example, we will replace “conservation agriculture achieved dynamic equilibrium” with language such as “after two decades of implementation, conservation agriculture produced soil conditions consistent with the approach toward a management-induced steady state described for systems managed >15 years (Caruso et al., 2018; West and Post, 2002).”
We will retain a more cautious discussion of equilibrium as a possible interpretive framework in the Discussion, since the literature on long-term conservation systems provides strong theoretical support for this trajectory. However, we will soften the framing where it reads as a confirmed finding and reduce the prominence of Tian et al. (2024), whose 10-year duration did not directly observe the >15-year mature phase we invoke. We will broaden the supporting literature and present the temporal interpretation more cautiously as a working framework.
Proposed Revision (Discussion, lines 443–454): “Our carbon accumulation patterns are consistent with the trajectory toward dynamic equilibrium described for conservation agriculture systems managed for 15–20 years (Caruso et al., 2018; West and Post, 2002). However, our cross-sectional design does not permit direct confirmation of equilibrium status, and the evolving management trajectory at this site (Section 2.2) means the system may still be on a trajectory of change. Additional temporal data would be valuable for resolving this question.”
2. Consistency in Treatment Presentation
Reviewer Comment: Figure 1 presents the results on aggregate stability for all four treatments. For consistency, the authors should either include the intermediate treatments throughout the paper or remove them from Figure 1.
Response: Figure 1 is intentionally designed to include all four treatments, and we consider it essential to the main text. The decision to focus subsequent analyses on CTCC and STNC was empirically motivated by prior work at this site (Araya et al., 2022), which tested all four treatments at 0–5 and 20–25 cm depths and found significant hydrological differences only between the two management extremes. Figure 1 provides independent corroboration of this pattern: aggregate stability data confirm that the intermediate treatments (CTNC and STCC) show limited differentiation from STNC, particularly in the 4–8 mm size class (Tukey HSD: CTNC vs. STNC, p = 0.112; STCC vs. STNC, p = 0.087). This figure gives the reader the empirical basis for the endmember analytical focus adopted throughout the rest of the paper.
We will add a brief statement in the Results section clarifying this rationale and citing Araya et al. (2022).
3. Statistical Tests and Block Structure
Reviewer Comment: The manuscript reports the use of Welch’s t-tests and Mann-Whitney U tests (Section 2.11). These tests do not account for block effects or the paired structure inherent in a randomized complete block design. A paired t-test, or a linear mixed model including block as a random factor would be more appropriate.
Response: We agree that accounting for the block structure of the experimental design will strengthen the statistical analysis. The CASI experiment employs a randomized complete block design with eight blocks arranged along a clay content gradient. For the two-treatment comparisons that constitute the bulk of the paper (CTCC vs. STNC, n = 7 paired blocks for soil cores, n = 6 paired blocks for density fractionation), we will adopt paired tests (paired t-tests where distributional assumptions are met, and paired Wilcoxon signed-rank tests where they are not) which directly honor the block structure. For the four-treatment aggregate stability comparison (Figure 1), we will use a randomized block ANOVA with Games-Howell post-hoc tests to accommodate unequal variances.
Block information is already tracked in our data, so this reanalysis is straightforward to implement. Given the large effect sizes observed for primary variables (e.g., 136% difference in aggregate stability, approximately 100% difference in surface carbon stocks), we anticipate that accounting for block structure will provide a more appropriate and robust assessment of treatment effects.
All p-values, significance indicators, and figure caption test references will be updated accordingly. The revised Section 2.11 will describe the updated statistical framework.
Proposed Revision (Section 2.11): “For two-treatment comparisons under the randomized complete block design, paired t-tests (pairing by block) were used where normality and variance assumptions were satisfied; paired Wilcoxon signed-rank tests were applied otherwise. For multi-treatment comparisons (Figure 1), randomized block ANOVA was followed by Games-Howell post-hoc tests to accommodate unequal variances. Statistical significance was denoted at p < 0.05 (*), p < 0.01 (**), and p < 0.001 (***).”
Specific Comments
4. Introduction Wordiness (Lines 75–86)
Reviewer Comment: Parts of the Introduction are somewhat wordy and could be streamlined. For example, the paragraph describing advances in soil analytical techniques (lines 75–86) appears redundant, as the methods applied in this study are largely standard and well established.
Response: Agreed. We will substantially condense this paragraph, retaining only the information necessary to motivate our specific analytical approach without overstating methodological novelty. The Introduction will be streamlined throughout.
5. Variable Sample Sizes Across Figures
Reviewer Comment: Sample sizes vary among analyses, for example eight replicates in Figure 1, seven for carbon stocks in Figure 5, and six for carbon fractions in Figure 7. Please explain the reasons for these differences, whether any samples were excluded, and the criteria used for exclusion.
Response: Sample size variation reflects different sampling strategies and the availability of material from specific blocks. Aggregate stability (Figure 1, n = 8 per treatment) used bulk samples from all eight replicate blocks. Soil core analyses (Figure 5, n = 7) had one replicate excluded due to sampling or processing issues. Density fractionation (Figure 7, n = 6) was performed on bulk samples from six of the eight blocks; blocks 7 and 8 were not sampled for this analysis. All six sampled blocks passed the ±10% mass recovery criterion described in Section 2.10.
We will add a paragraph to the Methods documenting the sample sizes for each analysis and the specific blocks included. We will also report mass and carbon recoveries for the density fractionation procedure (see also our response to Reviewer 2, Comment 14), including a sample-level table showing bulk carbon content, mass recovery, and apparent carbon recovery for each sample.
6. Figure Citation Error (Line 399)
Reviewer Comment: The figure citation here should refer to Figure 7.
Response: Thank you. We will correct this.
7. Additive Effects Claim (Line 423)
Reviewer Comment: Claims of additive effects require explicit comparison with tillage-only and cover-crop-only treatments. Without these comparisons, the interpretation remains speculative.
Response: We acknowledge this limitation. The synergistic interpretation is directly supported by the aggregate stability data (Figure 1), where all four treatments were compared and CTCC significantly exceeded both single-factor treatments. However, we cannot extend this interpretation to other variables where only the endmember treatments were analyzed. We will revise line 423 accordingly: “The aggregate stability data suggest synergistic rather than purely additive effects of combining reduced tillage with cover cropping (Figure 1), though this interpretation cannot be extended to variables where intermediate treatments were not directly compared.”
8. Equilibrium Language (Lines 443–454)
Reviewer Comment: Confirmation of a mature or equilibrium phase requires temporal data. Without time-series evidence, conclusions about reaching a stable phase should be softened.
Response: Agreed. This will be addressed as part of the reframing described in our response to General Comment 1.
9. Carbon Saturation Gap (Line 470)
Reviewer Comment: The large carbon saturation gap discussed here does not appear to represent a realistic or actionable target for conservation efforts in this system and should be framed more cautiously.
Response: We agree. The theoretical maximum from the Georgiou et al. (2022) framework represents an upper mineralogical bound that is not achievable under the environmental constraints of this Mediterranean system (low precipitation, seasonal aridity, limited carbon inputs during dry months). The system may have approached a management-induced steady state that is far below mineralogical capacity precisely because these environmental constraints, rather than mineral surface availability, limit carbon accumulation. We will revise this section to frame the saturation gap as indicating that mineral surfaces are not the primary constraint on carbon storage, rather than as unrealized sequestration potential. We will also propagate the uncertainty inherent in the Georgiou et al. framework (±9 mg C g⁻¹ mineral) through our calculations (see also our response to Reviewer 2, Comment 11).
10. Section 4.6 Wordiness
Reviewer Comment: The methodological insights are a bit wordy, given that these protocols are all standardized (line 556).
Response: Agreed. We will condense Section 4.6, focusing on the key finding that depth-stratified sampling is essential for detecting conservation agriculture effects and removing extended discussion of standardized protocols.
11. Streamlining the Conclusions
Reviewer Comment: Section 5 can be streamlined, in my opinion.
Response: Agreed. We will consolidate the Conclusions into a single cohesive section, removing the current subsection structure and focusing on principal findings and their direct implications.
Summary of Proposed Revisions
Global: Soften the strongest equilibrium assertions while retaining the interpretive framework; broaden literature base beyond Tian et al. (2024)
Section 2.11: Reanalyze with paired tests (pairing by block); randomized block ANOVA for Figure 1; add Games-Howell test description; update all figure caption test references
Methods: Document sample sizes and block coverage for each analysis; report mass and carbon recoveries for density fractionation
Introduction: Streamline, particularly lines 75–86
Results/Figures: Update all p-values and significance annotations; correct figure citation at line 399; add statement justifying the endmember focus with reference to Araya et al. (2022) and Figure 1
Discussion: Soften equilibrium claims; qualify additive effects interpretation; reframe carbon saturation gap as environmental constraint rather than unrealized potential; condense Section 4.6
Conclusions: Streamline into a single section
We believe these revisions will address the reviewer’s concerns while preserving the core contributions of the study. We look forward to the opportunity to submit a revised manuscript.
Citation: https://doi.org/10.5194/egusphere-2025-6047-AC1
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AC1: 'Reply on RC1', Teamrat Ghezzehei, 10 Apr 2026
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RC2: 'Comment on egusphere-2025-6047', Anonymous Referee #2, 17 Feb 2026
This manuscript will be a valuable contribution to our understanding of long-term conservation agriculture impacts in Mediterranean agricultural systems. The multi-method analytical approach of combining density fractionation, FTIR spectroscopy, aggregate stability, and comprehensive physical characterization is well-suited to the research questions. The figures are visually consistent and well-constructed, and the paper is engaging to read. The core finding, that sustained conservation management reorganizes carbon protection mechanisms toward aggregate-mediated physical protection while improving soil structural and hydraulic properties, is well-motivated and contributes meaningfully to ongoing discussions about carbon permanence and sequestration potential in dryland agricultural systems.
My principal comments are related to the dynamic equilibrium framing, the reporting of statistics, and management. I have listed general comments followed by specific comments below.
General comments:
The framing of the results as evidence that the soil system has reached "dynamic equilibrium" after 20 years is not supported by the study design. Demonstrating equilibrium requires temporal data showing that carbon stocks have stabilized, whereas this study provides a single time-point comparison after 20 years of divergent management, which is valuable on its own terms but cannot establish whether stocks are still changing. I recommend the authors reframe this language throughout, using the equilibrium concept as theoretical context drawn from the literature rather than a demonstrated outcome of this study. Related to this, the discussion leans heavily on Tian et al. (2024) as a basis for the temporal phases of carbon protection mechanisms. Although this reference is useful, it pertains to a different climate, soil type, and crop rotations, and it is also just one study. More significantly, citing it as the basis for the 0-5, 5-15, and 15+ year phase framework is problematic, because Tian et al. (2024) was a 10-year study, and so did not observe the mature phase beyond 15 years that the authors use to interpret the results. I recommend either citing literature that documents this, or being more cautious in how the temporal progression is framed.Relatedly, the discussion would benefit from addressing potential disconnects between the equilibrium framing and MAOC saturation. The authors assert that the system has reached management equilibrium and that much unsaturated mineral capacity remains. These are not mutually exclusive, but it's unclear how additional carbon will be sequestered to fill this capacity if management-related carbon sequestration has plateaued.
The characterization of the conservation treatment as a 20-year no-till experiment warrants more careful handling. As described in section 2.2, the no-till system permitted shallow cultivation for tomato crops from 1999-2011, with true no-till only achieved in 2012, meaning that for roughly the first 13 of the 20 study years, the system was more accurately described as reduced tillage than no-till. The paper's framing implies a consistency of management that is not supported by the methods. This has bearing on the equilibrium claim; if true no-till conditions were established relatively recently within the study period, the system could still be responding to that transition rather than having stabilized under consistent management. The authors should address this trajectory more explicitly, both in how they describe the treatment throughout the manuscript and in how they interpret the maturity of the soil system response.
Specific comments:
Throughout the manuscript, most results are presented as boxplots, which display medians and interquartile ranges. However, parametric tests comparing means (ANOVA, Welch's t-test) are reported for several variables. These are incongruent: where parametric tests are used, means with standard error bars would be the more appropriate display, and would also be more consistent with the error bar descriptions in several figure captions. The authors should either reconcile the figure types with the tests applied, or justify the mixed approach explicitly.
The Games-Howell post-hoc test appears in Figures 7 and 11 but is not mentioned anywhere in section 2.11. Please add it to the statistical methods description.
Figure 4 caption refers to a Wilcox test while the methods section describes Welch's t-test for two-group comparisons. Please reconcile.
The hydraulic conductivity results show a reversal between depths, with CTCC being higher at 0-5 cm and lower at 5-10 cm relative to STNC, that receives little discussion despite potentially meaningful implications for subsurface drainage and water redistribution. A brief interpretation would be useful.
The carbon retention efficiency estimate (19% of cover crop inputs retained) is a useful calculation but the denominator relies on estimated rather than directly measured cover crop biomass inputs over 20 years. This assumption should be stated explicitly and its uncertainty acknowledged.
Figure 4 caption cites a Wilcox test while the methods section describes Welch's t-test for two-group comparisons. Please reconcile.
The authors report MAOC saturation as point estimates but do not propagate the uncertainty inherent in the Georgiou et al. (2022) framework (±9 mg C g⁻¹ mineral) through their calculations. Given that this uncertainty represents roughly 10% of the central estimate, the saturation percentages carry uncertainty that could be reported. The authors' conclusion that both treatments remain well below theoretical maximum is likely robust to this, but reporting the propagated uncertainty would strengthen their conclusions.
Figure 8 presents proportional carbon and nitrogen distribution as stacked bars with no measure of variability, yet statistical comparisons between treatments are reported in the text for these proportions (section 3.5.3, p = 0.01 and p = 0.003). A reader has no way to visually assess the variability underlying those comparisons from the figure as presented. Error bars or an alternative figure type that conveys distributional information should be added.
Throughout the manuscript, significant figures are applied inconsistently. For example, aggregate stability is reported as 46.85 ± 15.22% alongside p-values carried to many decimal places, while other values are rounded to whole numbers. I recommend standardizing to reflect the actual precision of the measurements, following the conventions used elsewhere in this journal.
Citation: https://doi.org/10.5194/egusphere-2025-6047-RC2 -
AC2: 'Reply on RC2', Teamrat Ghezzehei, 10 Apr 2026
Manuscript egusphere-2025-6047: Two Decades of Conservation Agriculture Enhances Soil Structure, Carbon Sequestration, and Water Retention in Mediterranean Soils
Alvarez-Sagrero, Berhe, Chacon, Mitchell, and Ghezzehei
General Response
We thank Reviewer 2 for the thorough and insightful evaluation of our manuscript. We are grateful for the recognition that the multi-method analytical approach is well-suited to the research questions, that the figures are well-constructed, and that the core finding regarding reorganization of carbon protection mechanisms contributes meaningfully to ongoing discussions about carbon permanence. The principal comments regarding the dynamic equilibrium framing, treatment characterization, and statistical reporting are incisive and will substantially strengthen the manuscript. We address each point below.
1. Dynamic Equilibrium Framing
Reviewer Comment: The framing of the results as evidence that the soil system has reached “dynamic equilibrium” after 20 years is not supported by the study design. Demonstrating equilibrium requires temporal data showing that carbon stocks have stabilized, whereas this study provides a single time-point comparison… I recommend the authors reframe this language throughout, using the equilibrium concept as theoretical context drawn from the literature rather than a demonstrated outcome of this study.
Response: We agree that the strongest equilibrium assertions in the manuscript overstate what a cross-sectional comparison can support. We will revise the Abstract and Conclusions to present equilibrium as a plausible interpretation rather than a demonstrated outcome; for example, replacing “conservation agriculture achieved dynamic equilibrium” with “conservation agriculture produced soil conditions consistent with the approach toward a management-induced steady state described for systems managed >15 years (Caruso et al., 2018; West and Post, 2002).”
We will retain the equilibrium concept as an interpretive framework in the Discussion, since our 20-year dataset and the magnitude of the observed effects (136% aggregate stability improvement, ~100% surface carbon increase) are consistent with the literature on mature conservation systems. However, the framing will acknowledge the limitations of our design and note that the evolving management trajectory at this site (see Comment 4) provides an additional reason for interpretive caution. This reframing aligns with Reviewer 1’s General Comment 1.
2. Tian et al. (2024) Temporal Phase Framework
Reviewer Comment: Citing Tian et al. (2024) as the basis for the 0–5, 5–15, and 15+ year phase framework is problematic, because Tian et al. (2024) was a 10-year study, and so did not observe the mature phase beyond 15 years… I recommend either citing literature that documents this, or being more cautious in how the temporal progression is framed.
Response: This is an important point. We will: (a) explicitly acknowledge that Tian et al. (2024) did not directly observe the >15-year phase; (b) broaden the literature base with additional long-term studies documenting system behavior beyond 15 years (e.g., Caruso et al., 2018; West and Post, 2002, who reported declining carbon sequestration rates approaching equilibrium within 15–20 years across diverse systems); and (c) present the temporal phase interpretation as a working framework rather than an established trajectory, noting differences in climate, soil type, and cropping system between our site and the referenced studies
3. Disconnect Between Equilibrium Framing and MAOC Saturation
Reviewer Comment:The authors assert that the system has reached management equilibrium and that much unsaturated mineral capacity remains. These are not mutually exclusive, but it’s unclear how additional carbon will be sequestered to fill this capacity if management-related carbon sequestration has plateaued.
Response: This is a perceptive observation that identifies a logical tension we had not adequately addressed. We will add a paragraph to the Discussion making the following argument: the system may have approached a management-induced steady state that is far below mineralogical capacity precisely because environmental constraints, low precipitation, seasonal aridity, and limited carbon inputs during dry months, rather than mineral surface availability, limit carbon accumulation. The theoretical maximum from Georgiou et al. (2022) represents an upper mineralogical bound that is not achievable under these conditions. The saturation gap should therefore be interpreted as evidence that mineral surfaces are not the bottleneck constraining carbon storage in this system, rather than as unrealized potential under current management. Closing the remaining gap would likely require fundamentally different interventions (e.g., organic amendments, irrigation changes, deeper-rooted perennials) rather than continuation of the current conservation management
4. Treatment Characterization: Reduced Tillage vs. No-Till
Reviewer Comment: The characterization of the conservation treatment as a 20-year no-till experiment warrants more careful handling. As described in section 2.2, the no-till system permitted shallow cultivation for tomato crops from 1999–2011, with true no-till only achieved in 2012… The paper’s framing implies a consistency of management that is not supported by the methods… The authors should address this trajectory more explicitly.
Response: We agree that the treatment description requires more careful handling. The manuscript already uses the abbreviation CTCC (Conservation Tillage with Cover Crops), which accurately reflects the reduced-tillage character of the management. We will correct the few places where “no-till” is used casually in the Introduction and Discussion to be consistent with this terminology. More importantly, we will add a paragraph to the Discussion explicitly describing the management trajectory, reduced tillage with shallow cultivation for tomato crops (1999–2011) transitioning to true zero-tillage (2012–present), and acknowledging that true no-till conditions were established only approximately 7 years before sampling.
This management trajectory has two important implications for interpretation: (1) it directly supports our revised framing that equilibrium is a plausible trajectory rather than a confirmed outcome, since the system may still be responding to the intensification of disturbance reduction; and (2) it is representative of how conservation agriculture adoption typically occurs in practice (through incremental intensification rather than abrupt transitions) meaning our results capture a realistic adoption scenario.
Proposed Revision (Discussion): “The CT system permitted shallow cultivation for tomato crops from 1999–2011, with true zero-tillage achieved only in 2012 (Section 2.2). The system thus experienced approximately 13 years of reduced tillage followed by 7 years of true no-till before sampling. This management trajectory means our observations likely capture a system on a continuing trajectory of improvement rather than one fully equilibrated under consistent management. This progressive adoption pathway is, however, representative of real-world conservation agriculture implementation.”
5. Boxplots vs. Parametric Tests
Reviewer Comment: Throughout the manuscript, most results are presented as boxplots, which display medians and interquartile ranges. However, parametric tests comparing means are reported… The authors should either reconcile the figure types with the tests applied, or justify the mixed approach explicitly.
Response: We will justify the mixed approach. We retain boxplots with individual data points (jitter overlay) throughout because they transparently display data distributions, which we consider essential given our sample sizes (n = 6–7). At these sample sizes, boxplots provide the reader with a more honest picture of the data than bar plots showing only means and standard errors. Statistical inferences are based on paired tests (see Comment 8), and the specific test applied is reported in each figure caption. We will add a brief justification in Section 2.11 explaining this choice.
6. Games-Howell Post-hoc Test
Reviewer Comment: The Games-Howell post-hoc test appears in Figures 7 and 11 but is not mentioned anywhere in section 2.11. Please add it to the statistical methods description.
Response: We will add the Games-Howell test to Section 2.11.
7. Figure 4 Caption: Wilcox vs. Welch’s t-test
Reviewer Comment: Figure 4 caption refers to a Wilcox test while the methods section describes Welch’s t-test for two-group comparisons. Please reconcile.
Response: We will reconcile all figure captions with the statistical tests actually applied following the reanalysis with paired tests (see Comment 8).
8. Statistical Tests and Block Structure
Reviewer Comment: These tests do not account for block effects or the paired structure inherent in a randomized complete block design… A paired t-test, or a linear mixed model including block as a random factor would be more appropriate.
Response: Agreed. The CASI experiment uses eight blocks arranged along a clay content gradient. For the two-treatment comparisons that constitute the bulk of the paper (CTCC vs. STNC), block pairing is preserved: n = 7 paired blocks for soil core analyses, n = 6 paired blocks for density fractionation (six of the eight blocks were sampled for this analysis; see Comment 14 in Reviewer 1’s response for details on sample coverage). We will reanalyze using paired t-tests where distributional assumptions are met, and paired Wilcoxon signed-rank tests otherwise. For the four-treatment aggregate stability comparison (Figure 1), we will use a randomized block ANOVA with Games-Howell post-hoc tests. All p-values, significance annotations, and figure caption test references will be updated. This addresses the same concern raised by Reviewer 1 (General Comment 3).
9. Hydraulic Conductivity Depth Reversal
Reviewer Comment: The hydraulic conductivity results show a reversal between depths, with CTCC being higher at 0–5 cm and lower at 5–10 cm relative to STNC, that receives little discussion despite potentially meaningful implications for subsurface drainage and water redistribution.
Response: We will add a brief interpretation to the Discussion. The higher conductivity of CTCC at 0–5 cm likely reflects enhanced macroporosity from biological activity and root channels preserved by the absence of tillage. The reversal at 5–10 cm may reflect the absence of tillage-induced macropores that transiently increase conductivity under standard management, while the conservation system retains its undisturbed pore architecture. We note, however, that conductivity differences were not statistically significant at either depth due to high spatial variability (0–5 cm: p = 0.074; 5–10 cm: p = 0.284), and the interpretation should be understood as directional rather than conclusive.
10. Carbon Retention Efficiency Uncertainty
Reviewer Comment: The carbon retention efficiency estimate (19% of cover crop inputs retained) is a useful calculation but the denominator relies on estimated rather than directly measured cover crop biomass inputs over 20 years. This assumption should be stated explicitly and its uncertainty acknowledged.
Response: Agreed. We will explicitly state that the 19% retention estimate is based on cumulative estimated cover crop biomass inputs derived from periodic site-specific measurements extrapolated across the 20-year period, and acknowledge the uncertainty arising from year-to-year variation in cover crop productivity, composition, and decomposition. We will report the plausible range given known biomass variability at this site.
11. MAOC Saturation Uncertainty Propagation
Reviewer Comment: The authors report MAOC saturation as point estimates but do not propagate the uncertainty inherent in the Georgiou et al. (2022) framework (±9 mg C g⁻¹ mineral) through their calculations… reporting the propagated uncertainty would strengthen their conclusions.
Response: We will propagate the ±9 mg C g⁻¹ mineral uncertainty through our saturation calculations using the per-sample clay + silt data and report the resulting confidence intervals on saturation percentages. The conclusion that both treatments remain well below theoretical capacity is robust to this uncertainty, but reporting propagated intervals will provide more transparent assessment.
12. MAOC Saturation Hypothesis (Line 93)
Reviewer Comment: It is unclear why the authors hypothesize that the system is approaching a saturation limit for mineral-associated organic carbon, given the fine soil texture, relatively low carbon inputs, and dry climate.
Response: The reviewer is correct that our results showed the system is far from saturation, making the original hypothesis misleading. We will revise the hypothesis to state that we aimed to assess the degree of mineral-associated carbon saturation under long-term conservation management, without presupposing proximity to saturation.
Proposed Revision (line 93): “We hypothesized that long-term conservation management enhances aggregate-mediated physical protection of soil organic matter. We further assessed the degree of mineral-associated carbon saturation to evaluate whether mineral surface availability represents a primary constraint on carbon storage in this system.”
13. C=O Functional Group Assignment (Lines 267–268)
Reviewer Comment: The assignment of the C=O functional group as microbially derived organic carbon appears overly simplistic. There is evidence that other functional groups, such as amides and aromatics, may also contribute to signals in this range (Parikh et al. 2014), and the terminology should be revised or qualified.
Response: We agree. The 1660–1580 cm⁻¹ region encompasses C=O stretching of carbonyl groups but can also include contributions from amide I bands and aromatic C=C vibrations. We will revise the terminology to “processed organic matter” or “microbially-associated organic matter” and add a qualifying citation to Parikh et al. (2014).
14. Mass and Carbon Recoveries (Section 2.8)
Reviewer Comment: Please report mass and carbon recoveries for the fractionation procedure. This information is important for evaluating data quality and consistency.
Response: We will report a sample-level table including bulk carbon content, mass recovery, and apparent carbon recovery for all density fractionation samples. Mass recoveries were consistently within ±4% across both treatments (CTCC: 99.7 ± 3.1%; STNC: 100.5 ± 4.2%), confirming procedural integrity. Apparent carbon recovery showed greater variability (CTCC: 89.2 ± 6.4%; STNC: 81.8 ± 7.7%). This apparent carbon discrepancy reflects both dissolved organic carbon lost during SPT washing steps and heterogeneity in carbon content between the subsample used for bulk elemental analysis and the separate subsample used for fractionation. Within STNC, there is an apparent inverse relationship between bulk carbon content and carbon recovery. The worst recovery corresponds to the Block 5 (plot 19), which also had substantially higher C concentration than the mean.
Sample
Treatment
Block
Bulk C (%)
Mass recov. (%)
C recov. (%)
CTCC18-03
CTCC
1
2.36
98.2
97.2
CTCC18-08
CTCC
2
1.11
103.7
86.1
CTCC18-09
CTCC
3
1.52
96.1
88.0
CTCC18-15
CTCC
4
1.41
103.0
86.6
CTCC18-18
CTCC
5
2.03
100.0
81.0
CTCC18-24
CTCC
6
1.36
97.1
96.5
STNC18-02
STNC
1
1.16
98.1
85.2
STNC18-06
STNC
2
0.84
103.4
85.1
STNC18-11
STNC
3
0.85
104.4
87.0
STNC18-14
STNC
4
0.76
104.9
85.6
STNC18-19
STNC
5
1.55
96.2
66.4
STNC18-22
STNC
6
1.13
96.0
81.5
Samples from blocks 7 and 8 were not processed for density fractionation. All samples passed the ±10% mass recovery criterion described in Section 2.10.
15. Figure 2 Caption Typo
Reviewer Comment: There appears to be a typo indicated by two question marks.
Response: Thank you. We will correct this.
16. Comparative Language Without Statistical Support (Lines 348, 352)
Reviewer Comment: In several places, the manuscript uses comparative language such as “higher” or “lower” even when differences are not statistically significant. I recommend avoiding such terminology unless supported by statistical tests.
Response: Agreed. We will revise the Results to use neutral language (e.g., “did not differ significantly between treatments”) for all non-significant comparisons. Directional language will be reserved for statistically significant differences.
17. Figure 8: Variability in Stacked Bars
Reviewer Comment: Figure 8 presents proportional carbon and nitrogen distribution as stacked bars with no measure of variability, yet statistical comparisons between treatments are reported in the text… Error bars or an alternative figure type that conveys distributional information should be added.
Response: Agreed. We will revise Figure 8 to a grouped bar or boxplot format that displays the variability underlying the reported comparisons, with individual data points shown.
18. Significant Figures Consistency
Reviewer Comment: Throughout the manuscript, significant figures are applied inconsistently… I recommend standardizing to reflect the actual precision of the measurements, following the conventions used elsewhere in this journal.
Response: Agreed. We will standardize significant figures throughout, reporting means and standard errors to consistent decimal places within each variable, and p-values uniformly (three decimal places or p < 0.001).
Summary of Proposed Revisions
- Global: Soften the strongest equilibrium assertions while retaining the interpretive framework; correct casual use of “no-till” to match CTCC terminology; standardize significant figures; remove unsupported comparative language
- Abstract: Soften equilibrium claims
- Introduction: Revise MAOC saturation hypothesis (line 93); streamline analytical techniques paragraph
- Section 2.2: Add management trajectory description to the Discussion rather than revising the Methods, which already describe the history accurately
- Section 2.8: Report sample-level mass and carbon recoveries for density fractionation
- Section 2.11: Implement paired tests with block pairing; randomized block ANOVA for Figure 1; add Games-Howell description; justify boxplot retention; reconcile all test references in captions
- Results/Figures: Update all statistical annotations; revise Figure 8 to show variability; correct Figure 2 typo and line 399 citation
- Discussion: Add management trajectory paragraph; address equilibrium–MAOC saturation disconnect; broaden literature base beyond Tian et al. (2024); briefly interpret hydraulic conductivity reversal; acknowledge carbon retention efficiency uncertainty; propagate MAOC uncertainty; qualify C=O spectral assignment
- Conclusions: Streamline (also raised by Reviewer 1)
We believe these revisions will substantially strengthen the manuscript while preserving its core contributions. We look forward to the opportunity to submit a revised manuscript.
Citation: https://doi.org/10.5194/egusphere-2025-6047-AC2
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AC2: 'Reply on RC2', Teamrat Ghezzehei, 10 Apr 2026
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Jennifer Alvarez-Sagrero
Asmeret Asefaw Berhe
Stephany S. Chacon
Jeffrey P. Mitchell
Teamrat Afewerki Ghezzehei
The requested preprint has a corresponding peer-reviewed final revised paper. You are encouraged to refer to the final revised version.
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Alvarez-Sagrero et al. examine the combined effects of reduced tillage and cover cropping on soil structure, carbon storage, and organic matter composition. Overall, I do not have major concerns with the study. The narrative is generally coherent, the writing is easy to follow, and the data are clearly presented. Some sections of the Introduction and Discussion are somewhat wordy and could be streamlined, and a few inconsistencies in statistical treatment should be addressed. I provide general comments on the framing and analysis below, followed by additional specific comments.
My first general comment concerns the repeated use of the term “dynamic equilibrium” in the Abstract and Discussion (e.g., lines 6, 18, and 448). The authors argue that 20 years of conservation practices have led to the establishment of a new dynamic equilibrium. In my view, demonstrating a dynamic equilibrium typically requires time-series data showing stabilization of key variables, as was shown in Caruso et al. 2018 and Tian et al. 2024, both were cited by the authors. In the present manuscript, this inference is largely based on comparisons to other systems and on the assumption that 15 to 20 years is sufficient to reach equilibrium (line 448). While this is a reasonable hypothesis, it remains unclear whether the system has reached equilibrium or is still in the process of approaching it. This is not a critical flaw, but I would recommend softening the language. For example, the authors could emphasize that conservation agriculture can lead to such an equilibrium and that the observed differences are meaningful, while noting that additional temporal data, including future measurements or archived soil analyses, would be needed to confirm equilibrium status.
My second general comment relates to consistency in the statistical approach. In the Methods, the authors state that their primary comparison focuses on combined reduced tillage and cover cropping versus conventional tillage without cover crops, with intermediate treatments excluded due to limited effects (lines 176-180). However, Figure 1 presents the results on aggregate stability for all four treatments. For consistency, the authors should either include the intermediate treatments throughout the paper or remove them from Figure 1.
Relatedly, the statistical tests used to assess treatment effects deserve reconsideration. The manuscript reports the use of Welch’s t tests and Mann-Whitney U tests (Section 2.11). These tests do not account for block effects or the paired structure inherent in a randomized complete block design (line 106). A paired t-test, or a linear mixed model including block as a random factor would be more appropriate and would strengthen the statistical rigor of the study.
Specific comments:
Introduction: Parts of the Introduction are somewhat wordy and could be streamlined. For example, the paragraph describing advances in soil analytical techniques (lines 75-86) appears redundant, as the methods applied in this study are largely standard and well established.
Line 93: It is unclear why the authors hypothesize that the system is approaching a saturation limit for mineral-associated organic carbon, given the fine soil texture, relatively low carbon inputs, and dry climate. Later results indicate that observed carbon stocks are far below theoretical saturation levels. It is debatable whether these gaps represent realistic or achievable carbon sequestration potential in this system, and this point should be discussed more cautiously.
Lines 267-268: The assignment of the C=O functional group as microbially derived organic carbon appears overly simplistic. There is evidence that other functional groups, such as amides and aromatics, may also contribute to signals in this range (Parikh et al. 2014), and the terminology should be revised or qualified.
Section 2.8: Please report mass and carbon recoveries for the fractionation procedure. This information is important for evaluating data quality and consistency.
Figure 2 caption: There appears to be a typo indicated by two question marks.
Results, including lines 348 and 352: In several places, the manuscript uses comparative language such as “higher” or “lower” even when differences are not statistically significant. I recommend avoiding such terminology unless supported by statistical tests.
Sample sizes across figures: Sample sizes vary among analyses, for example eight replicates in Figure 1, seven for carbon stocks in Figure 5, and six for carbon fractions in Figure 7. Please explain the reasons for these differences, whether any samples were excluded, and the criteria used for exclusion.
Line 399: The figure citation here should refer to Figure 7.
Line 423: Claims of additive effects require explicit comparison with tillage-only and cover-crop-only treatments. Without these comparisons, the interpretation remains speculative.
Lines 443-454: As noted earlier, confirmation of a mature or equilibrium phase requires temporal data. Without time-series evidence, conclusions about reaching a stable phase should be softened.
Line 470: The large carbon saturation gap discussed here does not appear to represent a realistic or actionable target for conservation efforts in this system and should be framed more cautiously.
Section 4.6: The methodological insights are a bit wordy, given that these protocols areall standardized (line 556).
Section 5 can be streamlined, in my opinion.