Plant-Soil Feedback Effects on Germination and Growth of Native and Non-Native Species Common across Southern California

Round 1

Reviewer 1 Report

This is a carefully designed experiment to test the effects of conspecific and heterospecific soils on plant-soil feedback of a native shrub and two exotic annuals. By comparing their results to others, the authors conclude that there are experiment-specific and site-specific differences in response, making broad generalizations difficult at this stage.

 

In this study, soil from Artemisia decreased establishment of the mustard but not of the grass. The authors do not mention whether this conforms to observations in the field (is Bromus more abundant than Hirschfeldia under Artemisia?), or whether field observations or experiments are underway to decipher field patterns of establishment.

 

Although the seeds of B. nigra were substituted for Hirschfeldia in the experiment, I do not see this as a conceptual drawback, as both species are non-mycorrhizal and have similar phenology. B. nigra can be a larger plant (see Marushia et al. 2012 for a study on phenology of three annual mustard species).

 

Soil total N and C were measured in all treatments, which suggests that soil nutrients may not be an important factor on plant growth. The potential for differences in rate of mineralization, which was not measured, was discussed:

339 “sage scrub soil is more acidic than soils in non-native grasslands, which can have significant impacts on many ecosystem processes …..”

This is an interesting hypothesis. Soil pH is a simple measurement to make. Can you still measure soil pH on your samples to shed some light on this? Since you did not measure N turnover, but just total N, this would be of interest to help bolster your argument.

 

Most of my comments concern adding detail to Methods and some other small points.

 

Abstract l. 17, and Methods l. 99-100 “Bromus madritensis”

Do you mean red brome, B. madritensis ssp. rubens, or foxtail chess, B. madritensis ssp. madritensis? Be sure to specify. The Jepson Manual uses these names, but other sources (USDA Plants, Flora North America) use B. rubens for red brome and B. madritensis for foxtail chess. Your site is at an inland location, and is most likely to have red brome, B. rubens. But as written, it is unclear whether you have red brome or foxtail chess.

FYI, Fortune et al. (2008 AJB) show that B. rubens and B. madritensis have different ploidy levels and are likely not subspecies.

 

15 “dominate native”

CHANGE TO dominant native

 

60 Eriogonum fassiculatum,

correct spelling: fasciculatum

 

123 How much soil was used per pot?

124 “depot”

Do you mean Deepot? https://www.stuewe.com/products/deepots.php

What size Deepot was used?

 

136 “Transplanted seedlings had no above ground biomass.”

This is strange wording. I think you can delete this sentence.

 

149 What tests were performed to assess total bacteria and fungi? E.g., chloroform soil fumigation? You could cite the company website for methods.

 

183 You write that you did not assess bacterial activity, but line 149 says you did. If bacteria data were not provided, then delete bacteria from line 149.

 

158 PERMAMNOVA

correct spelling: PERMANOVA

 

216 “Brasica”

Correct spelling: Brassica

 

355 “terpintines”

I think you mean terpenes (ref 47)

 

References 17 and 20 are the same

 

Citations:

Fortune PM, N. Pourtau, N. Viron, and M.L. Ainouche. 2008. Molecular phylogeny and reticulate origins of the polyploidy Bromus species from section Genea (Poaceae). American Journal of Botany 95: 454-464.

Marushia, R. G., M. L. Brooks, and J. S. Holt. 2012. Phenology, Growth, and Fecundity as Determinants of Distribution in Closely Related Nonnative Taxa. Invasive Plant Science and Management 5:217-229.

Author Response

Response to Reviewer 1 Comments:

This is a carefully designed experiment to test the effects of conspecific and heterospecific soils on plant-soil feedback of a native shrub and two exotic annuals. By comparing their results to others, the authors conclude that there are experiment-specific and site-specific differences in response, making broad generalizations difficult at this stage. Thank you. This is indeed our goal and our main conclusion. We appreciate your detailed critique of the manuscript. We addressed all your comments and we think the manuscript has improved.

In this study, soil from Artemisia decreased establishment of the mustard but not of the grass.

1. The authors do not mention whether this conforms to observations in the field (is Bromusmore abundant than Hirschfeldia under Artemisia?), or whether field observations or experiments are underway to decipher field patterns of establishment. We added further information to highlight our observations in both the methods and discussion, but highlight that some observations were highlighted in the last paragraph of the introduction. Mustards and Bromus grasses are mainly relegated to disturbed areas and both are rare in intact sage scrub except along roads where disturbances are more common.

 

2. Although the seeds of  nigrawere substituted for Hirschfeldia in the experiment, I do not see this as a conceptual drawback, as both species are non-mycorrhizal and have similar phenology. B. nigra can be a larger plant (see Marushia et al. 2012 for a study on phenology of three annual mustard species). We agree. We added information from this reference and wording to clarify this point in both the methods and discussion, but we kept much of the previous language as there still may be differences with regard to germination and growth in con- and hereto-specific soils even with soils influenced by two mustard species.

 

Soil total N and C were measured in all treatments, which suggests that soil nutrients may not be an important factor on plant growth. The potential for differences in rate of mineralization, which was not measured, was discussed:

339 “sage scrub soil is more acidic than soils in non-native grasslands, which can have significant impacts on many ecosystem processes …..”

This is an interesting hypothesis. Soil pH is a simple measurement to make.

3. Can you still measure soil pH on your samples to shed some light on this? Since you did not measure N turnover, but just total N, this would be of interest to help bolster your argument. We agree that this information would bolster our argument. However, I have found it difficult to accurately measure pH myself. In addition, I currently do not have access to our pH meter as the shared lab is closed associated with COVID-19 precautions. However, we have had UC Davis measure pH in three previous studies. While we previously cited these experiments to support our ascertains, we now synthesized this information to include specifics measurements of pH in the different habitats.

 

Most of my comments concern adding detail to Methods and some other small points.

 

Abstract l. 17, and Methods l. 99-100 “Bromus madritensis”

Do you mean red brome, B. madritensis ssp. rubens, or foxtail chess, B. madritensis ssp. madritensis? Be sure to specify. The Jepson Manual uses these names, but other sources (USDA Plants, Flora North America) use B. rubens for red brome and B. madritensis for foxtail chess. Your site is at an inland location, and is most likely to have red brome, B. rubens. But as written, it is unclear whether you have red brome or foxtail chess.  We are conflicted here but mostly agree with the reviewer’s comment. We agree that the subspecies name needs to be included in the manuscript and have done that here the first time it is mentioned in the abstract and introduction. In addition, we have added some wording to the methods section. However, we refer to it as B. madritensis, the species name that is recognized as by the current Jepson Manual. We recognize that it used to be B. rubens, and maybe still should be referred to as B. rubens, but Jepson no longer recognizes that name, we list it as B. madritensis ssp. rubens. If the editor disagrees with this decision, we are open to rewording the manuscript.

FYI, Fortune et al. (2008 AJB) show that B. rubens and B. madritensis have different ploidy levels and are likely not subspecies. We added a sentence to highlight this taxonomic issue. Thank you for the reference.

 

15 “dominate native”, CHANGE TO dominant native

Thank you. This is haunts my writing.

 

60 Eriogonum fassiculatum, correct spelling: fasciculatum

corrected

 

123 How much soil was used per pot? We added the specific information requested (50 ml) – see below

124 “depot”, Do you mean Deepot? https://www.stuewe.com/products/deepots.php, What size Deepot was used? We actually used cone-tainers https://www.stuewe.com/products/rayleach.php. We referred to them as deepots in house, but have corrected the manuscript to be specific.

 

136 “Transplanted seedlings had no above ground biomass.”, This is strange wording. I think you can delete this sentence. Deleted

 

149 What tests were performed to assess total bacteria and fungi? E.g., chloroform soil fumigation? You could cite the company website for methods. We have added the requested information.

 

183 You write that you did not assess bacterial activity, but line 149 says you did. If bacteria data were not provided, then delete bacteria from line 149. Deleted. We wish we had done this, but were operating on an extremely limited budget for this project.

 

158 PERMAMNOVA, correct spelling: PERMANOVA corrected

 

216 “Brasica”, Correct spelling: Brassica corrected

 

355 “terpintines”, I think you mean terpenes (ref 47) corrected.

 

References 17 and 20 are the same reference 20 removed and applied to 17.

 

Citations:

Fortune PM, N. Pourtau, N. Viron, and M.L. Ainouche. 2008. Molecular phylogeny and reticulate origins of the polyploidy Bromus species from section Genea (Poaceae). American Journal of Botany 95: 454-464.

Marushia, R. G., M. L. Brooks, and J. S. Holt. 2012. Phenology, Growth, and Fecundity as Determinants of Distribution in Closely Related Nonnative Taxa. Invasive Plant Science and Management 5:217-229.

 

Reviewer 2 Report

The authors present an examination of soil-plant interactions in which they grew three plants in three soils with an established legacy of mono-dominant plant growth (one native and two invasive). They demonstrate differential effects of invasive conditioned soils on germination and growth rate of different plants, with Brassica nigra being the most responsive suggesting a biotic control. However, at times the level of inference is beyond what the data show; did the authors really demonstrate plant-soil feedbacks?. Further, language is a bit difficult to follow at times a rewrite of some sections would do much to improve the readability and flow of this MS, however, the MS is generally well-written as a whole.  Lastly, it is puzzling to me that the authors make not mention of arbuscular mycorrhizae here.  I believe that inclusion of this topic would do much to explain obtained results. Both Artemisia and Bromus are AM species while Brassica (and other mustards are not).  So long term establishment of Artemisia and Bromus would likely results in an enrichment of AMF and associated spores in the soil and AMF occurrence in known to affect brassica isotopic stoichiometry. I feel at least acknowledgement of this would be fair.

Lines 32-39:  I think this discussion would benefit from a slight expansion of plant-soil feedbacks and potential mechanisms including allopathy.

Lines 39-42: justification as to why plant-soil feedbacks might influence or be influenced by invasive is lacking here.

Lines 51-52: Expansion here on these mechanisms would be warranted.

Line 58: understanding invasion dynamics does not necessary allow the development of mitigation and restoration strategies.

Line 62: should this be ‘or were unaffected’?

Lines 64-66: Awkward wording

Lines 75-90: This section could be rewritten for clarity.  As written, it is a bit convoluted.

Lines 103-105 – this implies complete monoculture.  How close to a monoculture are these sites and is this consistent across seasons?

Lines 105-108 – Does that mean that all soils had the same N levels?  Was this tested?  What about legumes?  Where leguminous plants equally abundant?

Lines 112-113 – Undoubtably if there is a major pH difference.

Line 136: This is a puzzling sentence.

Lines 149-151: This seems out of place.  It might be moved up.

Lines 153-179: This section is oddly put. A rewrite to streamline text would improve it.  Also, in line 153 – it is stated that First a series of analyses were conducted but there is no ‘Second.’  Also, PerMANOVA seems like an odd choice to measure effects on C and N level given that you did not measure C and N from each terminal soil (after tests).  It is not necessarily incorrect, just unusual for these types of analyses.

Lines 184-187 (Table 1): Is it justified to use fungi and a proxy for bacterial activity?  I would argue not given generation time difference between these two and increased niche partitioning in bacteria.  Also, in Table 1 – are these values actually 0 or below detection limit?  It could be either, perhaps.

Figure 1: Given this figure (and associated text) it is unclear is unsterilized soils differed in C and N – this seems like the more ecologically relevant result.

Line 213 and throughout: Please include the den df for all PerMANOVA results.

Line 245 and throughout: I do not know if it has been demonstrated that these soils ‘resist’ B. nigra establishment per se.  Resist if an odd work and doesn’t really have a standard operation definition.  Please define this term carefully so that the reader knows precisely what these data represent.

Author Response

Response to Reviewer 2’s Comments

 

The authors present an examination of soil-plant interactions in which they grew three plants in three soils with an established legacy of mono-dominant plant growth (one native and two invasive). They demonstrate differential effects of invasive conditioned soils on germination and growth rate of different plants, with Brassica nigra being the most responsive suggesting a biotic control.

However, at times the level of inference is beyond what the data show; did the authors really demonstrate plant-soil feedbacks? Further, language is a bit difficult to follow at times a rewrite of some sections would do much to improve the readability and flow of this MS, however, the MS is generally well-written as a whole. Lastly, it is puzzling to me that the authors make not mention of arbuscular mycorrhizae here.  I believe that inclusion of this topic would do much to explain obtained results. Both Artemisia and Bromus are AM species while Brassica (and other mustards are not).  So long term establishment of Artemisia and Bromus would likely results in an enrichment of AMF and associated spores in the soil and AMF occurrence in known to affect brassica isotopic stoichiometry. I feel at least acknowledgement of this would be fair. We thank you for your comments and think your comments are astute. We have responded to the specific comments below which point out key areas where you think editorial changes are required, and we think we have improved the manuscript following your recommendations. In a few situations, we had a difficult time interpreting your recommendations and have done as best as we could. In general, we agree with most of your comments, but not those in the initial components of the introduction (we disagree with comments to line 58 and agree with all comments after that). We hope you understand. All comments have explanations to explain our actions.

We understand why the reviewer thinks that AMF should be acknowledged as the literature on AMF, particularly in sage scrub is intriguing. We have added some information in the discussion but have not highlighted AMF in our manuscript as: (1) We did not measure it directly and think that elevating AMF would add a significant level of conjecture, (2) AM colonization is often low at the seedling stage, particularly for two of the species studied here (Siguenza et al. 2006 – Plant Soil), and (3) while AMF may be playing a role, it is only one component of the soil microbiota and growth for all plant species is reduced in unsterilized soil indicating, at least to us, that deleterious interactions are stronger than positive mutualistic interactions, which I think our manuscript highlights or does more so now. If we are missing something, we would be happy to modify the manuscript.

Lines 32-39:  I think this discussion would benefit from a slight expansion of plant-soil feedbacks and potential mechanisms including allopathy. Do you mean allelopathy or allopathy?

Our approach to our introduction is to have a concise intro and then discuss potential mechanisms directly related to the patterns observed in the discussion. We do talk about allelopathy, AMF, changes in soil pH, influence of pathogens, etc. in the discussion.  

Lines 39-42: justification as to why plant-soil feedbacks might influence or be influenced by invasive is lacking here. We disagree. Our two sentences indicate that changes in plant assemblages influence multiple aspects if the soil environment and these changes can influence plant and germination and growth.

Lines 51-52: Expansion here on these mechanisms would be warranted. Explanation of the main factors influencing type-conversion N-deposition, fire and the grass-fire cycle are included.

Line 58: understanding invasion dynamics does not necessary allow the development of mitigation and restoration strategies. We agree. That is why we wrote “may provide valuable insights….”

Line 62: should this be ‘or were unaffected’? we added the verb.

Lines 64-66: Awkward wording On reflection, we agree. We think that use of “Conversely” and “In contrast” to start two sentences was indeed awkward. We changed the wording of these sentences to help clarify the complexity of these interactions for the readers.

Lines 75-90: This section could be rewritten for clarity.  As written, it is a bit convoluted. We agree and have edited the section making it more concise. We hope that these changes are consistent with the reviewer’s ideas.

Lines 103-105 – this implies complete monoculture.  How close to a monoculture are these sites and is this consistent across seasons? We made modifications to make it not seem as we are studying monocultures.

Lines 105-108 – Does that mean that all soils had the same N levels?  Was this tested?  What about legumes?  Where leguminous plants equally abundant? Again, we are not sure how best to address this. In this section, we are describing the sites. Later in the manuscript, we describe our soil testing in which we did test total N prior to the experiment. It was lower in the grassland as reported in Figure 1 and the results. Legumiminous plants are rare at our site. We have now included this statement. For clarification, Lupinus bicolor, is probably the most abundant in the grassland, but is difficult to find in the areas where we collected soil. Acmispon glaber is extremely common in burned areas and Acmispon strigosus is also much more common in burned areas than it is in any area we sampled for this experiment.

Lines 112-113 – Undoubtably if there is a major pH difference. We agree, but we do not think all readers will immediately make that link.

Line 136: This is a puzzling sentence. We made edits to make it more concise and we believe more clear.

Lines 149-151: This seems out of place.  It might be moved up. Okay – we moved it up. We initially put this here to focus more of the attention on the main aspect of the manuscript.

Lines 153-179: This section is oddly put. A rewrite to streamline text would improve it.  Also, in line 153 – it is stated that First a series of analyses were conducted but there is no ‘Second.’  We made some editorial changes to this section. We agree that it required some editorial work.

Also, PerMANOVA seems like an odd choice to measure effects on C and N level given that you did not measure C and N from each terminal soil (after tests). It is not necessarily incorrect, just unusual for these types of analyses. We disagree with it being an odd choice. PERMONVAs are permutation based analyses to test if treatments differ. We were testing if soil conditions differed among treatments prior to running the experiment. Tests following the experiment would test how soil treatments and plant and microbial activity influence soil nutrient concentrations.

Lines 184-187 (Table 1): Is it justified to use fungi and a proxy for bacterial activity?  I would argue not given generation time difference between these two and increased niche partitioning in bacteria.  Also, in Table 1 – are these values actually 0 or below detection limit?  It could be either, perhaps. We agree with this comment and admit that we may have overstepped. We have deleted that phrase. In a perfect world, we would have measured bacterial abundance and activity as well, but we had an extremely limited budget for this project

Figure 1: Given this figure (and associated text) it is unclear is unsterilized soils differed in C and N – this seems like the more ecologically relevant result. This is an astute observation. We have corrected this and included those comparisons as we did when examining growth. Thank you for making this observation.

Line 213 and throughout: Please include the den df for all PerMANOVA results. completed

Line 245 and throughout: I do not know if it has been demonstrated that these soils ‘resist’ B. nigra establishment per se.  Resist if an odd work and doesn’t really have a standard operation definition.  Please define this term carefully so that the reader knows precisely what these data represent We agree that we may have overstepped here. We have changed the wording in the ms including the abstract, discussion and conclusions.

Round 2

Reviewer 2 Report

I am satisfied with all manuscript changes in the revised submission.