NSF grant: EAR-0510726, Petrology and Geochemistry

Solar, G.S., Buffalo State College
Tomascak, P.B., SUNY Oswego

Reviews of the Proposal

Panel Summary:
A study of naturally occurring granitic melts of high-grade metamorphic rocks designed to understand the mechanisms of melt production, transfer and emplacement. Results will be useful in improving our understanding of melting processes of continental crust by observing small-scale macroscopic features in the field.

Intellectual Merit
Advancing knowledge

This study will consist of detailed, outcrop-scale field and geochemical studies utilizing teams of undergraduate students to map, measure, sample, and carry out analyses. This is a topic about which much is assumed, but about which little is known. The PIs have developed an important method by which field and geochemical data can be used to address leucosome/granite relationships. The pnael rated this RUI proposals very highly. The research plan is well constructed and carefully planned.

Creative and Original

These types of observations have been made for more than a century, but what is original is the attempt to match the macro-scopic observations with geochemical constraints.

Broader Impacts
Advance discovery while promoting teaching?

There will be intensive involvement of undergraduates which is carefully thought out and well-organized. The project will be a very enriching learning experience for undergraduates in the basics of field intensive research.

Summary: The panel recommends support for this proposal, if funds are available.

Panel Recommendation: Fund If Possible

Reviewer #1       Good

REVIEW:

The proposed work is aimed at testing ideas about migmatite formation and presumably related granite formation and the migration of granite magma through orogenic crust, as put forward for this region in previous work on these topics by the PIs. The results of the proposed work would provide additional information on the geometry of small to medium-scale structures in migmatites, and petrogrpahic, age, isotopic, and geochemical information on the migmatites and granites that will permit their relationship to be evaluated.

Given the nature of prior studies by the PIs in what appear to be rather similar rocks in western Maine, I would have appreciated a clearer statement of how the proposed work differs from the body of existing work, and how likely the results are to change what we know from prior work. I would also have liked to know, given that this work appears to be in an area that is along-strike from the prior studies in western Maine, how likely are the results to provide different information or a different perspective or tectonic context on the migmatite-granite relationship questions raised in the proposal.

The PIs do have a well thought out plan for involving a large number of undergraduates in this research, and for making it a meaningful and enriching experience. They are to be commended for that.

Reviewer #2      Very Good

REVIEW:

What is the intellectual merit of the proposed activity?

This proposal addresses a number of fundamental problems for our understanding of the linkages between melt generation, collection, and ascent. The PIs propose to attack these problems through numerous detailed field, petrographic, and geochemical studies of migmatites and potentially associated plutons at critical localities in the Central Maine metamorphic belt. The field studies will focus on the geometries of migmatites and related(?) plutons, and will be integrated with the petrographic, geochemical, and geochronological research. Much of the research will be carried out by undergraduate students under the close supervision of the PIs.

The proposal has a number of strengths. It raises important questions about migmatites and the flow of melt. Solar and Tomascak are well qualified to carry out the research and have a solid track record of publishing their data. They combine expertise in field-oriented structure and metamorphic petrology (Solar) with isotope geochemistry (Tomascak). Both have worked extensively on the migmatites and plutons of the central Maine metamorphic belt.

Despite these strong points, I have several concerns with the proposal.
1. This project builds on the earlier work of the PIs (particularly Solar's Ph.D. thesis) with Mike Brown at the University of Maryland. This research has led to numerous quality papers on the interrelationships of migmatites, plutons, and deformation in the region. From the proposal, it is not clear to me that the planned research will involve new avenues of inquiry, but rather will continue the same types of study of a larger area. Thus, it will probably lead to a better understanding of this specific migmatite belt, but it is less likely to result in any significant new insights into some of the fundamental questions on migmatites raised in the proposal.

2. The ages of migmatite leucosome crystallization versus pluton crystallization are critical for interpretations of melt collection, etc., as pointed out by the PIs. It is not clear that the PIs will be able to provide sufficiently precise geochronological data to test several of the major questions addressed in the proposal. Leucogranites are commonly difficult to date because of inheritance, and it would have been helpful if the PIs had more fully explored this and other issues in the proposal. The isotope lab at Syracuse is of high quality, but it is not clear that the PI will be able to devote the type of effort needed (CL imaging, numerous single grain fractions, etc.) to get the necessary age precision. A letter of support from Sampson (Syracuse) on the use of the lab was alluded to in the proposal, but I could not find it on fastlane.

3. I have concerns that the outcrops and topographic relief are not of sufficient quality to answer some of the questions posed by the PIs on the 3-D geometry of melt bodies. The stream exposures worked on by Solar are sufficient for some studies, but their lateral continuity and the relief are perhaps too limited.

The budget is very reasonable. I'd encourage the PIs to ask for buyout money to enable them to have more time to supervise the students.

What are the broader impacts of the proposed activity?

The strength of this proposal is the undergraduate research component. The PIs, and particularly Solar, have an exemplary record of mentoring undergraduate students on meaningful research projects. This is particularly noteworthy because Buffalo State is a commuter campus where it is commonly difficult for students to be involved in any activities beyond their course work and especially independent research. The PIs have also provided an unusually thorough plan for the undergraduate projects and have nicely displayed how the different student research projects will be integrated.

Summary Statement

This proposal focuses on important issues in melt generation, collection and flow in migmatites and will involve numerous undergraduate students in research. My overall rating is "very good", which I would break down into "good" for the intellectual merit and "excellent" for the broader impact.

Reviewer #3       Excellent

REVIEW:

What is the intellectual merit of the proposed activity?

Importance to the field: This proposal is to investigate the geometry and nature of the channels through which anatectic melt moved in contractional orogens. This subject lies at the very heart of where the study of crustal melting and melt migration, is presently active. The subject is also important in understanding how the earth's crust deforms and is able to sustain, or not sustain, regions of elevated topography in orogenic mountain chains, which is subject another that is in desperate need of field data to better constrain and add a physical dimension to the numerical models that are currently used. I know that the subject of this proposal is presently the focus of several research groups around the world, in Australia, Canada, France and Germany. The first serious attempts at resolving this problem were done in the late 1990s and the papers from these were published around 2000. Experimental studies on the same subject followed in the early 2000's and confirmed what the field work had revealed. Although workers now feel that they have an understanding of the how melt moves through the crust, one has to admit that that idea is based on results from just four small areas. Consequently, we do not yet know how general these observations and conclusions are and whether they apply to all cases of melting in the crust. To assess the general applicability we need studies from different tectonic settings. This study is one that will extend that small data base. So my view is that it this project is crucial to developing the field of knowledge concerned with the movement of granitic melt in the crust.

Quality of the investigators: The published work that Gary Solar has done with Brown at U. Maryland has been first class. In particular, I regard the two 1998 and the 2001 papers as being of the highest quality and extremely influential in the field. I was, therefore, very concerned that the field (my field) had lost one of its very brightest young researchers when Solar appeared to drop out of the publication game after his doctorate. I thought, and I still think, that Solar has the potential to be a world leader in his field. His unique quality is that he is an excellent structural geologist, and excellent metamorphic petrologist, especially in the field, and is more than a capable whole rock geochemist - I cannot think of any young researcher better equipped intellectually to accomplish the research goals set out in this proposal. I do not know Paul Tomascak, but I have read some of his work and found it thought provoking and enlightening; I am not qualified to judge his work on lithium, I have read it, but to my shame have to say it went over my head. The two investigators appear to have skills that complement one another, this encourages me to think that they can handle this project between them.

Creative and original ideas: Reading the proposal and comparing what has been already published on the subject I do not think that this is that much of an original proposal - although it is essential work. However, I can say from having taken part in the first round of studies on the subject of the geometry and evolution of melt flow channels in anatectic rocks, that there will be new and original results to report at the end of the study. These researchers will be able to recognize them and publish accordingly.

Organization: The proposal is well organized and the project summary easy to follow. The work they propose to do to accomplish the goals of the project is clearly set out and seem to be quite realizable. The plan to scout out new areas the year before is especially helpful and will ensure that students do not waste time on unsuitable areas.

Resources: I am surprised to find that both these researchers are at undergraduate colleges, their talents deserve better. They realize the limitations this poses on equipment resources and have found access at other establishments to the techniques they need. What I had not realized is that the undergraduate colleges do have one major resource, in large numbers of able and willing students looking for scientifically useful and challenging projects to work on. Thus, the investigators will have the hands available to get the project done. I hope NSF provides the financial resources.

What are the broader impacts of the proposed activity?

Teaching: The project as outlined will provide training through the projects and supervised field and lab work to at least eight students. The success rate in previous work is high, and if from the figures given two or three of these go on to graduate school, then the system will have benefited by receiving students with good backgrounds that have been instructed by highly motivated and able teachers.
Underrepresented groups: I cannot comment on this as I do not fully understand what is meant. I think a case could be made that scientists and engineers are an underrepresented group at universities these days. The way this project is set up will help to keep students in science at the post-graduate level and I see that as highly desirable.

Infrastructure: The project in not intended to augment to equipment infrastructure at either institution. However, it should lead to the development of a new research collaboration between the two colleges and the PIs in particular, and together, they could add a new dimension to understanding melt flow in orogens.
Dissemination: Students will be expected to present their results at regional and national Geological Society of America meetings. Both PIs have published important papers in the past, many of which have been in the top journals for their fields. I do not see any reason why that should not continue; they have the motivation and track record.

Summary Statement

I was very impressed with the work that Solar did for his Ph.D. and think that he has the potential to be world class in his field of deformed partially molten rocks. I sincerely hope that NSF gives this talented young researcher the opportunity to reach his potential. The objectives expressed in this project are those which other workers at the forefront of the filed are just considering or starting to do, so the project is highly topical.

Reviewer #4      Very Good

REVIEW:

What is the intellectual merit of the proposed activity?

This collaborative proposal describes a field-based project in Maine and New Hampshire that promises to determine how melt moves through the crust during regional contractional deformation. The PIs have identified exposures that are relevant to the goals of the project and have accumulated much data on the field relationships already. This accumulated data base should give them the ability to focus on the specific problem of melt transfer through the crust using migmatites and their relationship to granite plutons.

The problem of how melt moves through the crust is fundamental to our understanding of the deep crust of orogens. As such the results of this project, if successful, will be of interest to a wide range of researchers in many disciplines. The PIs appear to have a good grasp of the specific questions that need to be answered in order for the larger process of melt transfer through the crust to be understood. They also have shown that they are up to date on the current literature and know where the forefront of research is on this problem.

I would have liked to see more emphasis placed on the methodology and how the different components of the project, especially the field data, will be integrated with results from isotopic and microstructural studies. For example, we are told strain studies will be conducted but not how. Despite this, the integrated, multidisciplinary approach is a valid one and should help them achieve their goals. For these reasons I think the project should be funded if at all possible.

What are the broader impacts of the proposed activity?

The broader impacts of the proposed research center on giving research experience to teams of undergraduate students from two institutions. The students (and the PIs as well) will certainly benefit from the field and lab experiences. I would also encourage the PIs to plan field trips, incorporate the results into courses, convene workshops and special sessions etc. These also are important aspects of disseminating results and impacting the geosciences community.

Summary Statement

This proposal addresses an interesting problem centered on determining the mechanisms of melt transfer through the crust by using exposures of migmatite located in Maine and New Hampshire. The integrated field and analytical approach of the project is a potential strength of the proposed work. The project contains an excellent review of the problem. Some aspects, such as how strain in migmatites will be measured, are unclear but the PIs clearly have a good gasp of how to approach the problem and are qualified researchers. In general, this is a very good proposal that promises to yield important information about melt transfer and its relationships to granite plutons in orogens. The project should be funded if at all possible.

Reviewer #5      Very Good

REVIEW:

What is the intellectual merit of the proposed activity?

The PIs propose to conduct detailed, outcrop-scale field and geochemical studies of migmatitic and related rocks in western Maine and adjacent New Hampshire. They will use teams of undergraduate students to map, measure, sample, and analyze the relationships between leucosomes and melt migration during crustal melting. This is a topic about which much is assumed, but about which little is known. Solar, in particular, has provided an important method by which field and major/trace element data can be used to address leucosome/granite relationships, and Tomascak's isotopic expertise can greatly enhance such studies. Of all of the RUI proposals that I have read, I find this one to be the best constructed and planned. As one who has struggled with the same research topics, I think that the approach outlined here has a high chance of success.

What are the broader impacts of the proposed activity?

Understanding the timing, episodicity, and connectedness of magma networks in zones of crustal melting is essential in addressing questions about the sources of crustal melts, their migration through the crust, mechanisms of collection, and their influence of localization of strain. Many investigators emphasis either a regional perspective (e.g., Solar's original studies) or a grain-scale perspective. This research fills the gap between these two scales.
My institution has recruited graduate students from the New York system schools and we are commonly impressed by the preparation they receive. This is particulary true of those students who participate in honors or independent study. The value of such programs is well worth the effort expended by faculty and NSF.

Summary Statement

The PIs have identified a set of clear-cut scientific questions to address, they have identified (and used) the tools, they know how the students will be involved, and they have identified specific goals for the students. The budget is mostly reasonable, but could probably be trimmed slightly.

Reviewer #6 Excellent

REVIEW:

What is the intellectual merit of the proposed activity?

How important is the proposed activity to advancing knowledge and understanding within its own field or across different fields?

This project is significant in that it will examine the processes that control the extraction and transfer of magma in contractional orogens from the source region to the level of emplacement from a structural, geochemical, and isotopic perspective. The transfer of magma through the crust is likely to have a significant role in affecting crustal rehology Thus it will be important to understanding how the crust responds during protracted deformation events during periods of significant magma generation and transport. This is an issue that is significant to all researchers investigating orogenic events. In addition, the composition of igneous rocks is commonly used by many researchers to constrain the tectonic setting in which the magmatic activity and deformation occurred. Yet the extent to which the composition of the magma is inherited from the source region or significantly changed by processes operating during transport and emplacement are poorly understood. The PI's will be addressing this issue as well and have the potential to clarify the extent to which geochemical and isotopic characteristics of felsic rocks can be used in unraveling the geologic history of complex orogens. Because of these two aspects, the results of this study will be of broad interest to structural geologists, igneous petrologists, isotope grochemists, and tectonists throughout the world.

How well qualified is the proposer (individual or team) to conduct the project? (If appropriate, please comment on the quality of prior work.)

PI Gary Solar is highly competent, very knowledgeable, and well respected in the field of granite petrology. He has published several interesting and provocative papers on the interplay between crustal anatexis, deformation, and melt migration. It is impressive what he has been able to do without the benefit of NSF funding and while maintaining a heavy teaching load at an undergraduate institution. PI Tomoscak is also a highly respected isotope and innovative geochemist as well as an igneous petrologist. He has published several important papers as a result of his NSF funded research on lithium isotopes. He has also published several important papers concerning granite petrogenesis and regional tectonics from the Paleozoic orogenies in New England. The two PI's form a very strong team with complementary skills that are necessary to complete this project, and at the same time are both knowledgeable enough to prevent each other from straying too far!

To what extent does the proposed activity suggest and explore creative and original concepts?

This type of study needs to be done. It involves fundamental aspects of petrologic research; detailed field mapping, detailed petrography, geochemical and isotopic analysis of well characterized samples, and very careful geochronology. While none of this is original or creative, it is required to solve the problem.

I could suggest that since the PI's recognize the importance of constraining the third dimension to visualizing the connectivity of melt transfer pathways that highly precise computer field mapping techniques (e.g., reflectorless laser range finders, differential GPS units, GIS) may be useful in solving this problem. This approach may really help significantly in revealing the third dimensional connections at several scales (hand sample, outcrops, map scale). This is the only weak area in the proposal.

How well conceived and organized is the proposed activity?

The two PIs have considerable experience in this area, know the geology very well, and have published on it. Their work has stimulated considerable discussion and the PIs have designed a project that will test their ideas. The results of this work will advance the understanding of the processes operating during crustal anatexis, melt migration, and pluton formation during compressional orogenies. They have a clear, well organized plan for their field and laboratory work and while it may not be flashy, it is good solid fundamental petrologic techniques that are necessary to solve this problem. Both PIs have successfully completed and published on projects that require a similar approach. I am confident that with this kind of demonstrated experience both PIs will be able to successfully complete this project as well.

Is there sufficient access to the necessary resources?

Yes. PI Tomascak is in the process of setting up a clean lab at his institution and has good working relations with the isotopic geochemistry lab at the University of Syracuse. Other analytical data are being farmed out to the University of Washington. Both institutions have the other necessary equipment (computers, microscopes, rock saws, etc.) to complete the study.


What are the broader impacts of the proposed activity?

How well does the activity advance discovery and understanding while promoting teaching, training, and learning?

This proposal has very high merits on broader impacts because of the PI's great success with mentoring undergraduate research projects. Many of these students go on to attend graduate school or become Earth Science teachers. In either case, being involved in a quality research program provides them with many positive experiences which they will be able to apply in graduate school or incorporate into their K-12 teaching.

How well does the proposed activity broaden the participation of underrepresented groups (e.g., gender, ethnicity, disability, geography, etc.)?

This was not well established in the proposal. However, with the large number of undergraduate students mentored there is a very good chance that several of them meet these criteria.

To what extent will it enhance the infrastructure for research and education, such as facilities, instrumentation, networks, and partnerships?

This collaborative effort will enhance partnerships between three universities that should be sustained for many years to come given the successful working relationship the two PIs have enjoyed in the past. PI Tomascak is developing a clean lab which will greatly improve the efficiency of processing samples for isotopic work and will provide valuable experience for students planning on attending graduate school. I imagine several undergraduate students may continue on at Syracuse University for graduate work given the exposure to their facilities.

Will the results be disseminated broadly to enhance scientific and technological understanding?

The PI's have an excellent publication record and have lead field trips in this area. It is more than likely they will be able to continue their good work.

What may be the benefits of the proposed activity to society?

Training of a highly skilled scientific work force for K-12 teaching, industry, and for graduate school.

Summary Statement

I rated this proposal as Excellent for the following reasons: This is an important scientific problem, the mechanism by which melt is collected and transferred from the site of partial melting to the level of emplacement where it collects again to form a pluton, and the extent to which the geochemical and isotopic characteristics of the rocks in this pluton have been modified by these processes and can be used to infer characteristics of the original source material and tectonic setting in which the melt was generated. These issues have received considerable debate for a long time, and this debate will clearly benefit from the results of real honest to goodness detailed field work, petrography, and careful geochemical and isotopic analyses. The two PI's works very well together, have complimentary skills, and the necessary experience to successfully complete this project and publish the results. In addition, both PI's have success with providing a high quality research experience for many undergraduate students. Their students go on to graduate school (a substantial percentage) or become secondary school educators in the Earth Sciences. The only weakness I could see was the lack of incoprorating digital computer mapping techniques, which are excellent for such detailed outcrop studies, into their field work. They clearly could look into doing this as they work on this funded proposal.

Finally, in my opinion, given PI's Solar's strong publication record and success with mentoring undergraduate students as an Assistant Professor without external funding, he is clearly deserving of at least one funded proposal from the NSF before going up for tenure review.

Reviewer #7       Good

REVIEW:

What is the intellectual merit of the proposed activity?

The proposed work would yield potentially interesting results in terms of the timings of metamorphic and magmatic events and the connection (or not) between plutonic granites and migmatite formation. However, In my judgement, this proposeal is not really very innovative, in the sense that these problems have already received a reasonable amount of attention. It is not self-evident that the dating techniques to be employed have either the fine spatial or temporal resolutions needed to solve this question of timing and kinship between lithological units. There is also the wider question of whether studying bmelt formation and migration in a contractional setting, at this grade of metamorphism will yield results that are generally applicable to the problems of granite magma formation and migration.