the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 10 May 2021
The impact of soil development, rainfall intensity and vegetation complexity on subsurface flow paths along a glacial chronosequence of 10 millennia
Abstract. Hydrologic processes play an important role in the hydro-pedo-geomorphological feedback cycle of landscape evolution. Soil properties and subsurface flow paths change over time, but due to lack of observations important hydrologic processes such as water flow paths are often not properly considered in soil and landscape evolution studies. We investigated the evolution of subsurface flow paths during landscape development in the calcareous glacier forefield at the Griessfirn in the Swiss Alps. While the main focus was on flow path evolution and the formation of preferential flow paths with soil development, we also looked at the impact of irrigation intensity and vegetation complexity (in what way does the vegetation complexity defined by degree of vegetation cover and functional diversity at each age class relate to subsurface structures and flow path initialization?). We chose four glacial moraines of different ages (110, 160, 4 900, and 13 500 years) and conducted dye tracer experiments with Brilliant Blue (4 g l−1) on three plots at each moraine. The three plots at each age class differed by their degree of vegetation complexity (low, medium, and high) and each was further divided into three equal subplots where dyed water was applied with three different irrigation intensities (20, 40, and 60 mm h−1) and an irrigation amount of 40 mm. Dye pattern characteristics in form of volume density and surface area density were derived by digital image analysis and compared via statistical analysis.Volume density was used to classify the observed dye patterns into specific flow type categories. The effect of soil formation and thus changing soil characteristics on flow types were investigated by the analysis of structural and textural parameters in form of grain size distribution, porosity, bulk density, and loss on ignition. A change in flow types with increasing moraine age was observed from a rather homogeneous matrix flow to heterogeneous matrix and finger flow. Along the soil chronosequence, a reduction in particle sizes and an ongoing vegetation development resulted in an accumulation of organic matter in the topsoil and an increase in water storage capacity (decrease in bulk density and increase in porosity). Differences in irrigation intensity only had an effect on flow types at the oldest moraine, where the frequency of finger flow decreased with increasing irrigation intensity. A relation between vegetation complexity and flow types was only observed at the older moraines, which had a dense vegetation cover. With increasing vegetation complexity the proportion of preferential flow paths in form of finger flow also increased.
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RC1: 'Comment on hess-2021-242', Anonymous Referee #1, 09 Jun 2021
Reviewer comments on the paper “The impact of soil development, rainfall intensity and vegetation complexity on subsurface flow paths along a glacial chronosequence of 10 millennia” by Hartmann et al. submitted to HESS.
Having conducted research on subsurface flow, in particular preferential flow, for many years, I was very interested to review this paper. I always like to see such investigations that include detailed and well-planned field work. The senior author is commended for this detailed staining field work, but the linkages with other aspects of the study are weak and almost ad-hoc. Also, the planning of this study could have been improved (see comments that follow).
In reading through this paper, I found many similarities with the other two papers recently published by these authors (i.e., Hartmann et al., 2020a,b), one in this same journal and another in Earth System Sci. Data. We really need to be conscious about not republishing similar material; I am sure that was not the intent here, but this paper does come across as having at least some evidence of this issue. I fully realize that new infiltration studies were conducted as part of the paper I reviewed, but the authors did not do a good job in showing how these new findings helped address the key stated issue of the feedback cycle of the hydro-pedo-geomorphological system associated with these glacial chronosequences. As such, the current manuscript is overly wordy and repetitive, and poorly links the dye experiment with the vegetation complexes and soil properties, partly because of the mismatch of scales. Thus, I do not see this paper as acceptable in HESS and recommend that the authors carve out the new piece on the dye staining experiment and submit this elsewhere as a short note.
My more specific comments follow:
The Abstract of this paper needs to focus on the key findings. Currently it focuses most on methodology.
Section 1 – Introduction
Pg. 2, L. 12-13: The statement about preferential flow occurring more often at high rainfall intensities really depends on the environment you are working in and the type of preferential flow pathways that exist. In drylands where Hortonian overland flow dominates, few opportunities for subsurface preferential flow may exist, unless large cracks appear on the land surface that intercept surface runoff and route this into the subsurface.
Pg. 2, L. 19-28: This entire paragraph could simply be restated that most past chronosequence studies where soil development has been investigated are 2-dimensional – i.e., they only examine pedons, not 3-D flow paths, which is basically what was done in this study.
Pg. 2-3 last paragraph on pg. 2: You need a transition to this paragraph. Importantly, the reference to your previous and very similar paper in HESS (Hartmann et al., 2020a) summarizes that “observed flow types changed from a rather homogeneous rapid matrix flow in coarse material at the youngest moraine to a mainly finger flow at the medium-age moraines”. Given the small plots and the methods for establishing ‘horizontal connectivity’ among excavated slices of the profile (referenced in a difficult to access thesis), I am not convinced of the generalization you make – particularly the assumption that mainly finger flow occurs in ‘medium-age’ moraines. Given the heterogeneity that occurs in moraine material, there certainly could have been some preferential flow paths that were missed (at larger scales). Even in compact glacial tills, preferential flow can occur in glaciotectonic fractures and desiccation fractures. It seems to me that while your inferences related to vertical preferential flow are quite good, those related to what you call horizontal flow are rather suspect. I fully realize that such ‘horizontal’ pathways are difficult to quantify, but here you stress these differences. I really think you could have combined these two papers as they are closely related; this would have reduced the repetitive material in the two papers and made for a much more comprehensive story.
Pg. 3, L. 5-18: Here you spend an entire paragraph trying to justify why this paper is different from Hartmann et al. (2020a). In the previous paper, you also discuss vegetation effects, and I would pose the question: how is it possible not to consider vegetation (particularly below ground biomass) in discussions related to subsurface flow pathways? And the issue of irrigation intensity is not generalizable, as noted before.
Pg. 3, L. 19-23: This material belongs in the methods section.
Pg. 3, L. 24-28: Not a well-articulated objective statement if that was what this was intended to be.
Section 2.2: This entire section is very poorly connected with the stated objective related to subsurface flow paths. It is not clear why the ‘structural vegetation complexity measure’ was adopted, nor how this is linked to subsurface flow paths. The second paragraph begins with mentioning soil sampling, but then reverts to vegetation surveys; this is very disorganized and does not connect with subsurface flow. Many issues that seem not relevant to the discussion of subsurface flow are reported here, leaving me to wonder if this latter study (the one I reviewed) was an afterthought.
Section 2.3: It appears this dye study was conducted a year after the study reported in Hartmann et al. (2020a). However, the same plot design was used (subplots were 0.5 m x 1 m) and this raises the concerns I mentioned previously about difficulties in assessing horizontal preferential flow paths (especially across larger scales). These scale issues also affect other flow pathways, and this can be related to the variable infiltration rates used; the pathways that emerge may thus not be representative of larger scale behavior. Finally, no shortcomings of the Brilliant Blue dye methodology related to soil flow pathways was mentioned – this has been reported in numerous studies. At least this needs to be mentioned.
Section 2.4: Repetitive from the Hartmann et al. (2020a) paper which in turn was repetitive from Weiler (2001).
Section 2.5: It is completely unclear how disturbed soil samples and soil cores can help reconstruct subsurface flow pathways. Of course, they can give an indication of vertical soil water movement, but not horizontal pathways.
Section 2.6: Please remember, dye coverage does not equate to flux.
Section 3.1: I see no connection between these values of vegetation complexity and subsurface flow paths; again, this seems like data looking for a hypothesis link.
Section 3.2: Much of this section was already covered in the previous two papers by these authors and, once again, other than the connection made between selected soil properties and vegetation complexity, there is no connection to subsurface flow.
Section 3.3: These are the most interesting findings of this study and seem to be the most unique findings – i.e., not addressed in the previous two papers. That said, there remain issues of scale associated with the small size of these plots and how representative these are of the broader vegetation complexes and the inferences made herein. Possibly the authors could consider publishing only this part of the paper as a note. The rest of the paper does not strike me as unique. Also, as stated, this part only refers to vertical flow paths and thus has interpretative limits. Please see my comments in several places related to the artificial irrigation applications and the difficulties generalizing these findings as well.
Section 3.4: In an abbreviated version of the paper, which seems appropriate, this section would then be the Discussion. The scale limitations would need to be discussed here.
Section 4.1: This is mostly a rehash of older research, including what has already been presented in these authors papers. Most is not needed.
Section 4.2: Again, very little new here, compared to what these authors have previously reported. A much more concise version of the material presented from pg. 21, L. 32 to Pg. 22, L. 32 could be included in the Discussion of a modified note or paper, but much of the speculative material and inferences should be removed – e.g., some of the assumption about hydrophobicity, which was not tested.
Section 4.3 – Soil structure and texture: Again, this was somewhat covered in the authors prior papers. They mention the inadequacy of the two soil sampling locations relative to the vegetation complexes, and there is still no connection to subsurface flow. I feel this section adds very little.
Section 4.3 – Subsurface flow paths: This is mostly a repeat of what was presented earlier in this paper. It does not address 3-D flow, rather vertical pathways. Problems with the small plot size in glaciated terrain should have been anticipated prior to designing this experiment – e.g., the large boulders; pg. 25, L. 12-14). Furthermore, the description of the cause of overland flow that occurred during irrigation (pg. 25, L. 1-10 ) brings into question the artificial irrigation scheme; the explanation provided is does not address this, but rather focuses on the well-known process of surface sealing with no evidence presented. Also, why was this phenomon not observed in the previous study (again, not well explained)?
Section 4.4: You simply cannot compare the effects of different rain intensities in different biogeoclimatic areas and with different application methods. Thus, this section is of little value.
Section 4.5: Pg. 26, L. 9-13, Finally there is some mention of the drawbacks of using Brilliant Blue dye. Also, there is some acknowledgement of the obvious role that high energy water applications had on surface sealing (but why only in this study?) (pg. 26, L. 16-25). This was undoubtedly a major problem in this study design.
Section 5: All previous comments apply; in addition, while the statement on pg. 26, L. 30 may be true (“This shows that the influence of preferential flow paths increases with soil age”), the lack of robust 3-D evidence and a larger-scale perspective put this in question. I did not think the authors made a good connection (at appropriate scales) between vegetation complexity and subsurface flow paths, but now this is stated in the Conclusions as “We saw a direct relationship between vegetation complexity and subsurface flow paths at the old moraines and a relationship of vegetation complexity and soil properties at the 110, 4 900, and 13 500-year-old moraines” – this simply was not verified. Certainly, some inference could be made for vertical pathways, but even these were rather subjective. One of the concluding sentences – “…we still suggest that a more in-depth consideration of vegetation characteristics beyond coverage and land use types will provide useful insights for hydrological process research”, leaves the reader hanging and asking what was really accomplished here that was not reported in the previous two papers by these authors. And I do not see convincing evidence of the stated feedback cycle of the hydro-pedo-geomorphological system.
Citation: https://doi.org/10.5194/hess-2021-242-RC1 -
AC1: 'Reply on RC1', Anne Hartmann, 07 Jul 2021
The comment was uploaded in the form of a supplement: https://hess.copernicus.org/preprints/hess-2021-242/hess-2021-242-AC1-supplement.pdf
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AC1: 'Reply on RC1', Anne Hartmann, 07 Jul 2021
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RC2: 'Comment on hess-2021-242', Anonymous Referee #2, 20 Jul 2021
Hartmann et al. present a generally interesting study on infiltration capacities across a moraine chronosequence, where each chronosequence is divided into three levels of vegetation cover complexity and receives three different water application intensities, resulting in 36 different water applications. However, the experiment appears to be (more or less) a replica of a previous study (Hartmann et al. 2020a&b), with the main difference apparently being the parent material, which is calcareous in this manuscript and siliceous in the previous ones, and an apparent focus on vegetation and rainfall intensity influences. Even some of the figures are largely identical. It is not entirely clear to me what the new contribution of this manuscript is over the previously published study.
Additionally, I do have some concerns with the general study layout and possible interpretations. Each plot is divided into three 50cm wide zones with different rainfall application intensities. These zones are not physically separated from each other and to prevent interaction during application in one zone, the remaining two are covered. This still leaves room for interaction near the zone boundaries where water can be drawn laterally into the drier soil of a neighboring zone. The authors acknowledge as well (see below) that overland flow on some plots might have infiltrated near the zone boundaries, leading to increased infiltration there.
Then there is the question of the ages in the chronosequence. The two younger sites are 110 and 160 years old. 50 years difference is not much in a soil chronosequence, especially considering that the other soils are 4900 und 13000 Jahre alt. Unless I missed it, I did not see an explanation of what the authors expect in those 50 years to have happened to the soil.
If this were the authors’ sole publication on the topic, I would probably just consider major revisions (i.e., shortening and some restructuring). Given the other two publications, I am having difficulty seeing the novelty in this manuscript, though, and am unfortunately leaning toward rejection.
Some additional comments:
Moraines are a special type of cover and pedogenesis. Can you hypothesize what can be expected in soils that formed not from direct glacial processes?
Fig 5: Are the figures the mean of the five excavated profiles?
P21 L10-11: Is this purely based on the parent material or maybe also a function of landscape position, e.g., aspect, slope, etc.?
P22 L26-28: For the sake of comparability, would the “finger flow and macropore flow (high interaction)” class be classified as macropore flow in the previous study? (only based on patterns, even in the absence of actual macropores)
P22 L30-32: Given that the top layers contain hydrophobic material in both studies and no overland flow is observed, wouldn’t that suggest that most water should make it through this hydrophobic layer?
P26 L18-19: This raises a question about the experiment setup. If I understand correctly, the zones for different application intensities were neither separated by a non-irrigated space in between, not by some barrier installed into the soil profile that could have prevented surface flow onto the adjacent zone? If this is the case, couldn’t it be possible that the areas where the transition from one zone to the next happens simply receive more water than the rest of the zones? If deeper infiltration is observed below the transitions, that could be a result of more water infiltrating and thus being able to reach greater depths.
Citation: https://doi.org/10.5194/hess-2021-242-RC2 -
AC2: 'Reply on RC2', Anne Hartmann, 11 Aug 2021
The comment was uploaded in the form of a supplement: https://hess.copernicus.org/preprints/hess-2021-242/hess-2021-242-AC2-supplement.pdf
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AC2: 'Reply on RC2', Anne Hartmann, 11 Aug 2021
Status: closed
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RC1: 'Comment on hess-2021-242', Anonymous Referee #1, 09 Jun 2021
Reviewer comments on the paper “The impact of soil development, rainfall intensity and vegetation complexity on subsurface flow paths along a glacial chronosequence of 10 millennia” by Hartmann et al. submitted to HESS.
Having conducted research on subsurface flow, in particular preferential flow, for many years, I was very interested to review this paper. I always like to see such investigations that include detailed and well-planned field work. The senior author is commended for this detailed staining field work, but the linkages with other aspects of the study are weak and almost ad-hoc. Also, the planning of this study could have been improved (see comments that follow).
In reading through this paper, I found many similarities with the other two papers recently published by these authors (i.e., Hartmann et al., 2020a,b), one in this same journal and another in Earth System Sci. Data. We really need to be conscious about not republishing similar material; I am sure that was not the intent here, but this paper does come across as having at least some evidence of this issue. I fully realize that new infiltration studies were conducted as part of the paper I reviewed, but the authors did not do a good job in showing how these new findings helped address the key stated issue of the feedback cycle of the hydro-pedo-geomorphological system associated with these glacial chronosequences. As such, the current manuscript is overly wordy and repetitive, and poorly links the dye experiment with the vegetation complexes and soil properties, partly because of the mismatch of scales. Thus, I do not see this paper as acceptable in HESS and recommend that the authors carve out the new piece on the dye staining experiment and submit this elsewhere as a short note.
My more specific comments follow:
The Abstract of this paper needs to focus on the key findings. Currently it focuses most on methodology.
Section 1 – Introduction
Pg. 2, L. 12-13: The statement about preferential flow occurring more often at high rainfall intensities really depends on the environment you are working in and the type of preferential flow pathways that exist. In drylands where Hortonian overland flow dominates, few opportunities for subsurface preferential flow may exist, unless large cracks appear on the land surface that intercept surface runoff and route this into the subsurface.
Pg. 2, L. 19-28: This entire paragraph could simply be restated that most past chronosequence studies where soil development has been investigated are 2-dimensional – i.e., they only examine pedons, not 3-D flow paths, which is basically what was done in this study.
Pg. 2-3 last paragraph on pg. 2: You need a transition to this paragraph. Importantly, the reference to your previous and very similar paper in HESS (Hartmann et al., 2020a) summarizes that “observed flow types changed from a rather homogeneous rapid matrix flow in coarse material at the youngest moraine to a mainly finger flow at the medium-age moraines”. Given the small plots and the methods for establishing ‘horizontal connectivity’ among excavated slices of the profile (referenced in a difficult to access thesis), I am not convinced of the generalization you make – particularly the assumption that mainly finger flow occurs in ‘medium-age’ moraines. Given the heterogeneity that occurs in moraine material, there certainly could have been some preferential flow paths that were missed (at larger scales). Even in compact glacial tills, preferential flow can occur in glaciotectonic fractures and desiccation fractures. It seems to me that while your inferences related to vertical preferential flow are quite good, those related to what you call horizontal flow are rather suspect. I fully realize that such ‘horizontal’ pathways are difficult to quantify, but here you stress these differences. I really think you could have combined these two papers as they are closely related; this would have reduced the repetitive material in the two papers and made for a much more comprehensive story.
Pg. 3, L. 5-18: Here you spend an entire paragraph trying to justify why this paper is different from Hartmann et al. (2020a). In the previous paper, you also discuss vegetation effects, and I would pose the question: how is it possible not to consider vegetation (particularly below ground biomass) in discussions related to subsurface flow pathways? And the issue of irrigation intensity is not generalizable, as noted before.
Pg. 3, L. 19-23: This material belongs in the methods section.
Pg. 3, L. 24-28: Not a well-articulated objective statement if that was what this was intended to be.
Section 2.2: This entire section is very poorly connected with the stated objective related to subsurface flow paths. It is not clear why the ‘structural vegetation complexity measure’ was adopted, nor how this is linked to subsurface flow paths. The second paragraph begins with mentioning soil sampling, but then reverts to vegetation surveys; this is very disorganized and does not connect with subsurface flow. Many issues that seem not relevant to the discussion of subsurface flow are reported here, leaving me to wonder if this latter study (the one I reviewed) was an afterthought.
Section 2.3: It appears this dye study was conducted a year after the study reported in Hartmann et al. (2020a). However, the same plot design was used (subplots were 0.5 m x 1 m) and this raises the concerns I mentioned previously about difficulties in assessing horizontal preferential flow paths (especially across larger scales). These scale issues also affect other flow pathways, and this can be related to the variable infiltration rates used; the pathways that emerge may thus not be representative of larger scale behavior. Finally, no shortcomings of the Brilliant Blue dye methodology related to soil flow pathways was mentioned – this has been reported in numerous studies. At least this needs to be mentioned.
Section 2.4: Repetitive from the Hartmann et al. (2020a) paper which in turn was repetitive from Weiler (2001).
Section 2.5: It is completely unclear how disturbed soil samples and soil cores can help reconstruct subsurface flow pathways. Of course, they can give an indication of vertical soil water movement, but not horizontal pathways.
Section 2.6: Please remember, dye coverage does not equate to flux.
Section 3.1: I see no connection between these values of vegetation complexity and subsurface flow paths; again, this seems like data looking for a hypothesis link.
Section 3.2: Much of this section was already covered in the previous two papers by these authors and, once again, other than the connection made between selected soil properties and vegetation complexity, there is no connection to subsurface flow.
Section 3.3: These are the most interesting findings of this study and seem to be the most unique findings – i.e., not addressed in the previous two papers. That said, there remain issues of scale associated with the small size of these plots and how representative these are of the broader vegetation complexes and the inferences made herein. Possibly the authors could consider publishing only this part of the paper as a note. The rest of the paper does not strike me as unique. Also, as stated, this part only refers to vertical flow paths and thus has interpretative limits. Please see my comments in several places related to the artificial irrigation applications and the difficulties generalizing these findings as well.
Section 3.4: In an abbreviated version of the paper, which seems appropriate, this section would then be the Discussion. The scale limitations would need to be discussed here.
Section 4.1: This is mostly a rehash of older research, including what has already been presented in these authors papers. Most is not needed.
Section 4.2: Again, very little new here, compared to what these authors have previously reported. A much more concise version of the material presented from pg. 21, L. 32 to Pg. 22, L. 32 could be included in the Discussion of a modified note or paper, but much of the speculative material and inferences should be removed – e.g., some of the assumption about hydrophobicity, which was not tested.
Section 4.3 – Soil structure and texture: Again, this was somewhat covered in the authors prior papers. They mention the inadequacy of the two soil sampling locations relative to the vegetation complexes, and there is still no connection to subsurface flow. I feel this section adds very little.
Section 4.3 – Subsurface flow paths: This is mostly a repeat of what was presented earlier in this paper. It does not address 3-D flow, rather vertical pathways. Problems with the small plot size in glaciated terrain should have been anticipated prior to designing this experiment – e.g., the large boulders; pg. 25, L. 12-14). Furthermore, the description of the cause of overland flow that occurred during irrigation (pg. 25, L. 1-10 ) brings into question the artificial irrigation scheme; the explanation provided is does not address this, but rather focuses on the well-known process of surface sealing with no evidence presented. Also, why was this phenomon not observed in the previous study (again, not well explained)?
Section 4.4: You simply cannot compare the effects of different rain intensities in different biogeoclimatic areas and with different application methods. Thus, this section is of little value.
Section 4.5: Pg. 26, L. 9-13, Finally there is some mention of the drawbacks of using Brilliant Blue dye. Also, there is some acknowledgement of the obvious role that high energy water applications had on surface sealing (but why only in this study?) (pg. 26, L. 16-25). This was undoubtedly a major problem in this study design.
Section 5: All previous comments apply; in addition, while the statement on pg. 26, L. 30 may be true (“This shows that the influence of preferential flow paths increases with soil age”), the lack of robust 3-D evidence and a larger-scale perspective put this in question. I did not think the authors made a good connection (at appropriate scales) between vegetation complexity and subsurface flow paths, but now this is stated in the Conclusions as “We saw a direct relationship between vegetation complexity and subsurface flow paths at the old moraines and a relationship of vegetation complexity and soil properties at the 110, 4 900, and 13 500-year-old moraines” – this simply was not verified. Certainly, some inference could be made for vertical pathways, but even these were rather subjective. One of the concluding sentences – “…we still suggest that a more in-depth consideration of vegetation characteristics beyond coverage and land use types will provide useful insights for hydrological process research”, leaves the reader hanging and asking what was really accomplished here that was not reported in the previous two papers by these authors. And I do not see convincing evidence of the stated feedback cycle of the hydro-pedo-geomorphological system.
Citation: https://doi.org/10.5194/hess-2021-242-RC1 -
AC1: 'Reply on RC1', Anne Hartmann, 07 Jul 2021
The comment was uploaded in the form of a supplement: https://hess.copernicus.org/preprints/hess-2021-242/hess-2021-242-AC1-supplement.pdf
-
AC1: 'Reply on RC1', Anne Hartmann, 07 Jul 2021
-
RC2: 'Comment on hess-2021-242', Anonymous Referee #2, 20 Jul 2021
Hartmann et al. present a generally interesting study on infiltration capacities across a moraine chronosequence, where each chronosequence is divided into three levels of vegetation cover complexity and receives three different water application intensities, resulting in 36 different water applications. However, the experiment appears to be (more or less) a replica of a previous study (Hartmann et al. 2020a&b), with the main difference apparently being the parent material, which is calcareous in this manuscript and siliceous in the previous ones, and an apparent focus on vegetation and rainfall intensity influences. Even some of the figures are largely identical. It is not entirely clear to me what the new contribution of this manuscript is over the previously published study.
Additionally, I do have some concerns with the general study layout and possible interpretations. Each plot is divided into three 50cm wide zones with different rainfall application intensities. These zones are not physically separated from each other and to prevent interaction during application in one zone, the remaining two are covered. This still leaves room for interaction near the zone boundaries where water can be drawn laterally into the drier soil of a neighboring zone. The authors acknowledge as well (see below) that overland flow on some plots might have infiltrated near the zone boundaries, leading to increased infiltration there.
Then there is the question of the ages in the chronosequence. The two younger sites are 110 and 160 years old. 50 years difference is not much in a soil chronosequence, especially considering that the other soils are 4900 und 13000 Jahre alt. Unless I missed it, I did not see an explanation of what the authors expect in those 50 years to have happened to the soil.
If this were the authors’ sole publication on the topic, I would probably just consider major revisions (i.e., shortening and some restructuring). Given the other two publications, I am having difficulty seeing the novelty in this manuscript, though, and am unfortunately leaning toward rejection.
Some additional comments:
Moraines are a special type of cover and pedogenesis. Can you hypothesize what can be expected in soils that formed not from direct glacial processes?
Fig 5: Are the figures the mean of the five excavated profiles?
P21 L10-11: Is this purely based on the parent material or maybe also a function of landscape position, e.g., aspect, slope, etc.?
P22 L26-28: For the sake of comparability, would the “finger flow and macropore flow (high interaction)” class be classified as macropore flow in the previous study? (only based on patterns, even in the absence of actual macropores)
P22 L30-32: Given that the top layers contain hydrophobic material in both studies and no overland flow is observed, wouldn’t that suggest that most water should make it through this hydrophobic layer?
P26 L18-19: This raises a question about the experiment setup. If I understand correctly, the zones for different application intensities were neither separated by a non-irrigated space in between, not by some barrier installed into the soil profile that could have prevented surface flow onto the adjacent zone? If this is the case, couldn’t it be possible that the areas where the transition from one zone to the next happens simply receive more water than the rest of the zones? If deeper infiltration is observed below the transitions, that could be a result of more water infiltrating and thus being able to reach greater depths.
Citation: https://doi.org/10.5194/hess-2021-242-RC2 -
AC2: 'Reply on RC2', Anne Hartmann, 11 Aug 2021
The comment was uploaded in the form of a supplement: https://hess.copernicus.org/preprints/hess-2021-242/hess-2021-242-AC2-supplement.pdf
-
AC2: 'Reply on RC2', Anne Hartmann, 11 Aug 2021
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