There has been outstanding productivity associated with the co-PI's prior support in terms of publications.
Prior support has resulted in the contribution of genomic resources and computational approaches to the maize genetic community. There has also been notable training of underrepresented groups resulting in published work.
If this is a resubmission, how have previous reviews been addressed? N/A
The proposed work capitalizes on the genomic resources and past work available to the maize community. Clearly the system is one of the model systems to quantify the role of introgressive hybridization in adaptation and more specifically how maize has been domesticated to be productive outside of its ancestral range of domestication.
A major criticism is centered on the collection of phenotypic data from the three proposed common garden plots. First, the location of all three plots is not confirmed with two sites described as potential and the third to be identified at a later date. Second, not enough detail is provided on the methodology of collecting the phenotype data. However, the most important criticism is that maternal effects are not adequately controlled in the common garden experiments. To collect seeds from plants grown in different field sites and then to use them as the replicates to determine the genetic component of trait variation/expression does not meet the standard of quantitative genetic protocol that partitions genetic from environmental factors. Additionally, there were several criticisms focused on the genomic approaches. The primary concern is that the genomic scans of admixtured populations likely will reduce the precision of locus location because of linkage disequilibrium. A second concern is that genome content varies among domesticated varieties of maize and this may introduce challenges in the analyses of ancestry, if the same phenomenon is found in nondomesticated Zea.
Additionally, the panel felt that the PIs could do a better job explaining the novelty of the work for a broader evolutionary genetics community.
The strongest aspect of BIs is the international collaboration and travel available to the greaduate student participants.
Several weaknesses were identified. First, while undergraduates are to be recruited into the co-PI's lab, no funding for this purpose is allocated in the proposal. Lack of funding may bias the types students that will be available for recruitment. However, to temper this criticism, the same lab does have a fine record of increasing minority participation in research. Concern was also raised about the lack of leveraging of the ISU GK-12 program. The panel would like a better description of the work load associated with graduate student participation in this program. The postdoc mentoring plan should be strengthened by addition of details.
The data management is fine.
N/A
The panel is excited by the question of the role of introgressive hybridization in the evolutionary process but the PIs did not make a strong case that their system and approaches stand out among the current investigations. The panel felt that the lack of control of maternal effects for the common garden experiments is a serious issue that must be addressed before the phenotypic data can be interpreted genetically. The Broader Impacts need to be more fully developed.
The panel recommendation is: Not Competitive
This summary was read by the assigned panelists and they concurred that the summary accurately reflects the panel discussion.
Panel Recommendation: Not Competitive
This proposed research would examine genome-wide effects of hybridization in the genus Zea. The PIs would examine variation in introgression across the genome, test whether hybrids are favored in the hybrid zone, and test for selection on traits and loci in these hybrid zones. Furthermore, the importance of introgression during the post-domestication spread of maize will be examined. Although I like this proposal, I have one substantive concern (about maternal effects), as well as several suggestions for improvements in revision.
If I understand correctly, maternal effects will be addressed by environmental covariates at the collection sites, but trait measurements will be conducted with plants grown from field collected seeds spanning an environmental gradient. This does not control for maternal effects, hence evolutionary genetic conclusions would be compromised.
For the proposed molecular population genetic analyses of natural selection: These have the usual problems with testing for soft sweeps. How will these be addressed? (Is it possible that domestication might reduce this problem?)
For Objective IC, an association analysis will be conducted with trait and GBS data. What is the scale of LD in these hybrid zone populations? Will admixture in these hybrid zones lead to false negatives for GWAS?
This work is justified as an attempt "to characterize the evolutionary role of hybridization and introgression in this system and more generally describe how these processes can shape genomes." While I agree that this is interesting, what fundamental, unanswered evolutionary questions will be resolved by these experiments? And what are the advantages of this system compared to comparable studies of hybridization in fish or sunflower or whatever? What is unique about this system that will move our evolutionary understanding forward to new levels?
This proposal would be improved by a detailed discussion after each experiment or aim about potential problems and their solutions. In addition more discussion is needed after the experimental section about how results will be integrated with the questions, leading to specific conclusions about the main questions. Don't leave the reviewers to figure this out. Instead, explicitly tell us something like "if data show pattern X, then we will conclude Y about this evolutionary hypothesis."
Given his current generous funding from NSF, involvement of co-PI Ross-Ibarra reduces the likelihood of funding for this proposal, and reduces the independence (and therefore the likelihood of tenure) for Hufford. I suggest a more tightly focused proposal submitted by Hufford alone.
The broader impacts are strong.
I think this proposal has a lot of potential, and I would be strongly supportive of a revision that addressed these issues.
The PIs are strong scientists with great expertise in this area.
Not only is maize an important agricultural crop supporting millions of people, it has also been an important model system for understanding the process of domestication and basic evolutionary processes. This project seeks to leverage hybridization between wild relatives of maize and between them and maize to understand the nature of gene flow between taxa and the role it might play in adaptation and geographic spread. A mixture of genotyping by sequencing and common garden experiments will assess at a genomic level the porosity of hybrid zones and whether differences across the zones are adaptive. Both of these are inherently important issues. Genotyping by sequencing will also be used to assess whether adaptive introgression into Z. mays from wild relatives aided its geographic spread, also an important issue. While an exciting goal, the predictions associated with this are entirely one sided, i.e., of the form "if it has occurred, we expect this narrow set of results." There is no assessment of whether those results could occur by other means or what other outcomes would indicate.
Broader impacts include international collaboration and student exchanges with the Eguiarte lab at UNAM and student/postdoc training. Importantly, one of the graduate students involved in the project will also be engaged in Iowa State U.'s GK12 Fellowship program and thereby able to bring his/her science into the middle or high school classroom one day each week.
In summary, this project leverages an important biological system that has contributed a great deal to our understanding of plant evolution, domestication, and (as an important food crop) human history. The potential for broader impact via international exchange is high. However, at least one set of experiments is being set up without a clear mapping between the possible outcomes and the alternative interpretations. As a result, these may not be particularly definitive in expanding our understanding.
This proposal uses genomic approaches and leverages existing genomic tools to quantify the amount of introgression between two subspecies of Zea, parviglumis (lowland and progenitor of modern corn) and mexicana (highland), perhaps via Zea mays, and use common garden experiments to identify which morphological and phenological traits have diverged through selection between parviglumis and mexicana. Association analyses will be used to identify the genomic regions associated with the above traits. Furthermore, the team proposes to quantify introgression from one other teosintes and another species of Zea, both found in tropical climates, into mays. This will be the first assessment of the role of hybridization with these additional subspecies/species as facilitating the range expansion of mays into tropical environments. Introgression, if detected, from these tropical subspecies should overlap with QTL that have been identified as the genetic basis for growing under these warmer tropical conditions. The overall goal of the proposed activities is to better understand the role of hybridization and introgression as either leading to the evolution of isolating barriers or as a creative role in evolution through the introduction of new genetic variation and gene combinations. Because most of the study taxa are subspecies of the same species, the scope of the questions is limited to addressing long gene flow events at the within species level.
The team has the resources and knowhow to conduct the genetic surveys and determine the amount of hybridization and introgression. Although it is not clear whether their story can be translated to more natural systems that do not include a domesticated species as a possible bridge, understanding the genetic origins of teosintes and the role of hybridization with other Zeas is clearly important, given the economic impact and social relevance of corn to human societies. Thus this proposal has a very clear broader impact simply because it proposes to quantify the sources of genetic variation that have led to modern corn.
The genomic methods are well described but less well described are the methods for phenotyping, found in the data management plan. Sites for the common garden at this time, in part reflecting the uncertainty of safely working in the study areas and have not been determined.
The team is very well poised to complete the genomic work and have access to the resources to do so. However, the field phenotyping is less concrete.
The research team has a track record with mentoring undergraduate and graduate students. There will be extensive exchange between the US and Mexican labs providing valuable international research experience. The proposal is very specific in defining the ways the labs will interact on a regular remote basis, further serving the students and postdocs involved with the project. The ISU GK12 Fellowship program is another clear strength of the broader impacts within this proposal.
The proposed work primarily addresses the role of hybridization and introgression among teosinte subspecies as a source of genetic variation and adaptation to local climatic conditions. The work will also investigate the role of hybridization and introgression from another Zea species into Zea mays as potentially facilitating the ability of humans to grow corn under tropical conditions. Because of the genomic resources and methods available to corn researchers, they have the potential to document hybridization and introgression at very fine genetic scales, and therefore may more broadly inform us of how both contribute to evolutionary process. Much of the BI is anchored on well mentoring the junior scientists and the participation of the PI with the ISU GKL12 program.
The proposed research is aimed at determining the history of, and adaptive importance for, hybridization and introgression between subspecies of Zea mays, and between Zea mays subspecies and domesticated maize.
Aim 1 focuses on two hybrid zones between parviglumis (low elevation) and mexicana (high elevation). From dense sampling across hybrid zones, high density SNP data will be generated through a 'genotyping by sequencing' approach. These data will be used to assess genomic regions of introgression and genomic regions for which a history of selection is evident. Through a set of common garden experiments spanning one of the parviglumis/mexicana hybrid zones, the PIs will test whether a set of variable traits are potentially adaptive across the elevational gradient. Association analyses will inform whether any of the phenotypic variation across the elevational gradient can be connected to genotypic variation. Results from integrating these two components are potentially quite exciting for future studies aimed at better understanding the genetic basis of adaptations in an economically important lineage.
Aim 2 uses the same types of genomic data and analyses (tests for introgression/selection) to determine the extent of introgression between zea mays subspecies and domesticated maize. The primary question that will be answered with these data is whether introgression genomic regions from Zea into maize facilitated spread of cultivated maize into diverse habitats.
The PIs are well qualified to undertake the proposed research, but critically, they have extensive collaborative relationships with researchers in Mexico who will be fundamental for completing the research objective - from a necessary collecting trip in year 1 to the common garden experiments later in the proposed timeline.
The population genomic approaches outlined in aim 1 and 2 are appropriate, as are the common garden experiments.
One of the broader impacts of the proposed research will be the exchange of graduate students between institutions in Mexico and the labs of the PIs in the US. This is a well-developed and very exciting component of the broader impacts - facilitating an international experience for young scientists. However, I have some problems with the other two broader impacts described in the proposal.
The PIs propose to train undergraduates through this research project. They state that they will train students who 'volunteer' to work in their labs and do not suggest any other mechanism for supporting these students (funds in the budget for Iowa State to support 1 undergraduate per year, but not the UC Davis budget). Restricting the training of undergraduates in labs primarily to those who can volunteer likely reduces the socioeconomic diversity of students in the lab. The proposed broader impacts would be strengthened by undergraduate training through university programs that provide stipends for students to gain research experience, especially students from underrepresented groups in STEM fields, or through future REU supplements to this grant.
The 3rd broader impact is the participation of graduate students being trained on this grant in K-12 programs where they would spend 1 day a week for 1 year in local schools, with (I suspect) extensive prep work on other days. This sort of commitment might make it difficult during that year for a graduate student to be research productive. Some indication of anticipated hours in the program compared to a standard GTA position would help to alleviate concerns one might have about the ability of the student to succeed in research while participating in this intensive outreach program.
Results from the proposed research will provide novel insights into the history of Zea and the role of diversity within wild Zea mays for facilitating the successful spread of domesticated maize through habitats of Mexico and Guatemala. I am surprised that some of these questions, especially with respect to introgression between maize and zea mays are unanswered, perhaps due to limitations in generating high density SNP data. The outcomes of the proposed research seem timely and of broad interest. Aspects of the Broader Impacts could be modified for improvement.
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What is the potential for the proposed activity to advance knowledge and understanding within its own field or across different fields (Intellectual Merit)?
Strengths: The proposed activities have the potential to dramatically increase our understanding of how hybridization and introgression shape genomic variation across different time-scales. The results will be highly relevant for understanding adaptation, and also have agricultural applications.
Weaknesses: None.
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To what extent do the proposed activities suggest and explore creative, original, or potentially transformative concepts?
Strengths: None.
Weaknesses: None.
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Is the plan for carrying out the proposed activities well-reasoned, well-organized, and based on a sound rationale? Does the plan incorporate a mechanism to assess success?
Strengths: All aspects of the proposed activities are well-reasoned and sound. By studying a crop species and its wild relatives the PIs will be able to leverage substantial resources and address meaningful questions in evolutionary biology. The molecular and analytical methods suggested are among the best available. The PIs are clearly aware of potential issues that could arise in data analysis, and, for example, are prepared to analyze the data even if sequence coverage is low by working directly with genotype likelihoods.
Weaknesses: None.
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How well qualified is the individual, team, or institution to conduct the proposed activities?
Strengths: The PIs are highly qualified to conduct the proposed activities. They have substantial experience with the proposed methods and with the study system, and they have a demonstrated history of success.
Weaknesses:
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Are there adequate resources available to the PI (either at the home institution or through collaborations) to carry out the proposed activities?
Strengths: The PI has adequate resources to carry out the proposed activities.
Weaknesses: None.
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What is the potential for the proposed activity to benefit society or advance desired societal outcomes (Broader Impacts)?
Strengths: The proposed activities will advance education by leveraging an existing fellowship program to bring graduate students into middle school and high school classrooms. This will help provide the secondary students with authentic science experience and facilitate training of the graduate students.
Weaknesses: None.
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To what extent do the proposed activities suggest and explore creative, original, or potentially transformative concepts?
Strengths: None.
Weaknesses: None.
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Is the plan for carrying out the proposed activities well-reasoned, well-organized, and based on a sound rationale? Does the plan incorporate a mechanism to assess success?
Strengths: Clear methods exist for assessing the success of the proposed broader impacts.
Weaknesses: None.
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How well qualified is the individual, team, or institution to conduct the proposed activities?
Strengths: The PIs are qualified to carry out the proposed activities.
Weaknesses: None.
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Are there adequate resources available to the PI (either at the home institution or through collaborations) to carry out the proposed activities?
Strengths: The PIs have the resources needed for the proposed activities.
Weaknesses: None.
The proposed research will analyze the genomic consequences of hybridization and introgression in Zea (domesticated maize and its wild relatives) with an emphasis on the outcomes of hybridization at two different time scales. This results will shed light on hybridization's role in structuring genomic variation and in adaptation. The proposed methods are very well thought out and the project has a high chance of success. The proposed broader impacts are meaningful and are also likely to succeed.
The proposal clearly lays out previous research on hybridization in Zea and the evolutionary questions that can be addressed with the system. The focal questions in the proposal are relevant to understanding the basis of genetic discontinuities between subspecies or species. The combination of DNA sequencing from large numbers of individuals and measurement of phenotypes and genetic variation in reciprocal transplants is particularly appealing. Likewise, the combination of study of hybridization in parapatric teosintes and between cultivated and wild Zea will lead to novel insights. Overall, the research is likely to provide a large amount of valuable empirical data and analyses of the role of hybridization in shaping adaptive variation in Zea.
The investigators have strong research records, are highly likely to succeed in their objectives, and have the research facilities and collaborative agreements to facilitate the work.
The proposal did not make very strong connections between focal questions and critical analyses. Whereas some categorical predictions were given for alternative models, it seems likely that reality will be more complex than discrete alternatives and clearly recognizable introgressed haplotypes. Likewise, in the description of analyses of ancestry, comparisons are described, but the bases for inference are somewhat vague. Consequently it was difficult to evaluate the extent to which this research would go beyond gathering a lot of data that pertain to interesting questions, and would also lead to strong inferences with broader implications. Nevertheless, I have confidence that the research will lead to novel insights and that the team is well-poised to collect and analyze the data.
While these questions can be addressed in this system, there are substantial challenges that are particular to this system. For example, given genome content variation among maize cultivar lines (e.g., lines only sharing ~50% of their genomes), why should we not be concerned about the difficulty of comparing teosintes, particularly in the context of hybridization? This seems like it would be a particular challenge for analyses of ancestry, as portions of individual genomes will not be comparable (because they are simply lacking in some individuals and present in others). Similarly, while the genetic map order has been found to be stable at a coarse scale, should the recombination rate variation among parents in the NAM not lead to concern about the modeling of recombination?
The broader impacts of the proposal are well-articulated, concrete, multi-faceted and realistic. The research will lead to outreach activities in middle or high school classrooms and to training of graduate and postdoctoral researchers within laboratories and through an exchange program with collaborating research labs in Mexico. The objectives fit the proposed research and personnel well.
None noted.
This proposal will lead to novel insights regarding the relationship of hybridization and local adaptation among teosintes. These findings should articulate well with other studies that are addressing similar questions in other systems.