Documentation to "My Case"

Panel Summary # 1

Proposal Number: 0308362

Panel Summary:

The P.I. proposes three tasks to be performed in a multi-anvil appatus: (1) extend phase equilibrium studies on the CaO-MgO-Al2O3-SiO2 system to Fe-bearing compositions at 7-24 GPa, (2) equilibrate inclusions in diamond (e.g., pyroxene) at deep mantle pressures and temperatures to try and infer its P-T condition of origin, and (3) explore the stability of chromite and the equilibrium concentrations of Cr in all important phases potentially coexisting in the mantle with chromite. Most reviewers find the proposed work on inclusions in diamond to be the most interesting, whereas there is mixed reaction to the other two research tasks proposed. More than one reviewer points out that the P.I. has ignored the work of many others, including experimentalists working on similar topics (e.g., diamond inclusions) at high pressures with multi-anvil devices. The budget is extremely high (full support for the P.I. and a post-doc), with little justification for the post-doc. The proposal would be improved if the P.I. cited the work of others, and came up with a reduced budget (perhaps by focusing on only the second task and eliminating the post-doc salary). The panel does not recommend funding of this proposal.

Panel Recommendation: Do Not Fund

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Review #1
PROPOSAL NO.: 0308362
INSTITUTION: SUNY Stony Brook
NSF PROGRAM: PETROLOGY AND GEOCHEMISTRY
PRINCIPAL INVESTIGATOR: Gasparik, Tibor
TITLE: Experimental Investigation of the Origin of Inclusions in Diamonds From the Deep Mantle
RATING: Fair

REVIEW:
What is the intellectual merit of the proposed activity?

An extremely difficult proposal to review in the context of supporting a major experimental facility on the basis of the unfinished work of a single PI. While a great admirer of the earlier contributions of the PI, this proposal does NOT meet his prior intellectual standards. Part 1 is to "extend"; part 2 is to "continue"; and although part 3 is "new", it is narrow and unconvincing in addressing a major issue in mantle petrology and
geochemistry.

What are the broader impacts of the proposed activity?

The broad impacts of the proposed scientific activity are unlikely to add significantly to our knowledge of the mineralogy and geochemistry of the upper mantle. The continued existence of the high pressure facility at Stony Brook is a separate and ill-placed issue here; it may still have some impact but its glory is tarnished as competing instumentation has improved and techniques have advanced.

Summary Statement

The PI is complimented in his valient effort to extend the life of a major experimental facility; however, the proposed science to achieve this end lacks imagination and justification.

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Review #2
PROPOSAL NO.: 0308362
INSTITUTION: SUNY Stony Brook
NSF PROGRAM: PETROLOGY AND GEOCHEMISTRY
PRINCIPAL INVESTIGATOR: Gasparik, Tibor
TITLE: Experimental Investigation of the Origin of Inclusions in Diamonds From the Deep Mantle
RATING: Very Good

REVIEW:
What is the intellectual merit of the proposed activity?

This proposal outlines a program of high pressure research aimed at improving our understanding of the phase stabilities on the Earth's upper mantle down into the uppermost part of the lower mantle. As the PI states this work is the only direct way to obtain information about the solid phases that are stable in the deep earth. The work will follow previous research of the PI by extending phase relations determined in simple systems to systems of greater chemical complexity. This experimental study will provide fundamental input to costrain models of the constitution of the earth's mantle. What are the broader impacts of the proposed activity? Improved interpretation of geophysical measurements and other remote sensed data that is used to infer properties of the Earth's upper mantle, transition zone and uppermost part of the lower mantle. Also, the work will alow us to broaden our interpretation of the possible types of chemical differentiation processes that have led to stratification of the Earth's mantle.

Summary Statement

The PI has been a sustained contributor to the field of experimental mineral physics for the last 15 years. This proposal represents an effort to remain active in that field. This reviewer has not been privy to the workings of COMPRES and/or the internal politics of SUNY/Stony Brook, and as a result this proposal mystifies more than it clarifies. Why is there no support for the PI at SUNY? The costs are high, and the PI does not justify support for a post-doc, though he does justify continued support for himself. One wonders why Stony Brook has not done something to help keep the PI on staff, or why he did not follow COMPRES to whereever it went.... but the tone of the proposal might provide part of the answer. There is much good science proposed by the PI, but it is mixed with overly dramatic claims and hyperbole that make it difficult to know how to react to the good work that is in the proposal. The PI has something to add to the high pressure experimental community, but it is hard to know how how he will make it on his own. My score of very good is a mix of excellent for the good science that is proposed averaged with a fair for the vagueness and lack of appropriate citation for other contributors in the high pressure mineral physics field.

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Review #3
PROPOSAL NO.: 0308362
INSTITUTION: SUNY Stony Brook
NSF PROGRAM: PETROLOGY AND GEOCHEMISTRY
PRINCIPAL INVESTIGATOR: Gasparik, Tibor
TITLE: Experimental Investigation of the Origin of Inclusions in Diamonds From the Deep Mantle
RATING: Fair

REVIEW:
What is the intellectual merit of the proposed activity?

The PI proposes to continue his experimental exploration of high-pressure mineral phase relations in simple systems. Plans are to expand upon existing NCAMS work to include Fe and Cr, and to investigate some Mg-Fe-(-Ca) end-member systems, some of which are pertinent to understanding diamond inclusions. While the goals of understanding the bulk composition effects on mantle mineralogy are extremely important, the strategy suggested certainly represents the long route to attaining such goals. Indeed, after the 1700+ experiments carried out over two decades by the PI, we are still at n = 4. It will clearly take some time before we reach n = 10-11, for a more complete description of the major components that affect phase assemblages and compositions. As an example of the limitations of this approach, there is the PI's proposal to examine Fe on the stability of Mj - by examining phase relations in the En-Di-Hd-Fs (Mg-Fe-Ca-Si) system. Numerous high-pressure experiments on natural bulk compositions, though, show that Mj does not exist independent of aluminous garnet; instead, these two components exhibit a solid solution relationship. Mj (in- Al garnet) must therefore be affected by other competing garnet components, which will include elements such as Na, Cr, Ti, Mn and Al. The proposed experiments, though, will not only yield only a small advance in understanding garnet solid solutions at high pressure, it will do so at a very high cost. The only advantage is that some thermodynamic constraints can be extracted from simple systems. But there are very large errors in thermodynamic quantities extracted (as coefficients) from models of such experiments, even when the experimental errors are much less, as in piston cylinder work. A more rapid track, clearly, would be to examine natural peridotite bulk compositions. While I have little enthusiasm for the studies outlined in section 1., the proposed work regarding diamond inclusion mineralogy and the solubility of Cr is interesting. The PI unfortunately does not acknowledge the work of Harlow, Luth, Irifune, Frost and many other researchers undertaking multi-anvil work on compositions relevant to diamond inclusions. This would have been a much stronger proposal had the PI placed the significance of his work into a broader context of existing experiments and problems. Nevertheless, an investigation of compositions analogous to those found in the inclusions of the Stachel et al work (KK-83) should be enlightening, and probably worth funding. In addition, we still have yet to understand the origin of very Cr-rich garnets, and the proposed exploration of chromate solubility could be quite valuable (not so much for enhancing the NCMAS thermodynamic data set, but for understanding the genesis of Cr-rich phases in diamond inclusions). Regarding the experimental procedures, the proposed use of seeds is an intriguing tactic to establish an approach to equilibrium, which is always difficult in such experiments. The claim that thermal gradients can be used to advantage, though, is questionable. One always hopes that at a very localized level mineral-melt or mineral-mineral exchange equilibrium is approached. But mass transport effects (at the very least solubility gradients, if not Soret diffusion) related to thermal gradients creates problems for experiments that require the maintenance of bulk composition (as in section 1). And again, the PI fails to cite relevant work . in this case Lesher and Walker (1988, JGR), which significantly precedes Gasparik and Drake (1995). The quoted thermal gradients (200 oC across the sample) seem very low, and I wonder if the experimental difficulties are being understated. These are difficult experiments, and their difficulty should not preclude funding, but it is very important that experimentalists be fully forthcoming about the limitations of this kind of work. In addition, the costs of these multi-anvil experiments seem excessive, and indicate that carbide cubes are consumed in every experimental run. My impression is that new techniques employed by groups at Houston, U. of AZ and in Japan have circumvented the need for such high rates of carbide consumption.

What are the broader impacts of the proposed activity?

There is no doubt that the PI has performed a large number of experiments, with some relevance to mantle petrology. And undoubtedly, some graduate students have learned some experimental procedures useful to the material sciences. These are valid implications of this work. I am uncertain as to the value of further exploration of simple end-member systems. These kinds of projects can yield some useful (albeit very imprecise) thermodynamic information, but this approach represents a very slow route to understanding mantle mineralogy. If such data could be obtained at lesser cost, then I could support the pursuit of such work. But considering the great expense of such experiments, NSF would probably do best to spend its limited resources on projects of greater potential impact.

Summary Statement

I would be hesitant to fund the study of end-member systems since only a small advance in our understanding of mantle mineralogy is gained at considerable expense. On the other hand, those projects related to chromite saturation and diamond inclusions are interesting, and could perhaps be funded, at a greatly reduced level. I otherwise feel that these projects represent far too great an allocation of resources to support just one faculty
and at best a very small research group. It should also be noted that the proposal as a whole seems to neglect the work of experimentalists not associated with Stony Brook (both in regards to scientific problems and experimental techniques); this casts a poor light on the proposal as a whole. If this proposal were to be rejected and then re-submitted, I would strongly urge the PI to consider placing his science and experimental techniques into a broader context. While the PI surely feels obliged to show the quantity and significance of his work, such efforts should not be at the expense of recognizing the work of highly productive and talented
scientists outside the Stony Brook circle.

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Review #4
PROPOSAL NO.: 0308362
INSTITUTION: SUNY Stony Brook
NSF PROGRAM: PETROLOGY AND GEOCHEMISTRY
PRINCIPAL INVESTIGATOR: Gasparik, Tibor
TITLE: Experimental Investigation of the Origin of Inclusions in Diamonds From the Deep Mantle
RATING: Excellent

REVIEW:
What is the intellectual merit of the proposed activity?

The proposed research includes a diverse range of projects related to phase equilibria in the mantle, and addresses a number of long standing problems. In particular, the conditions under which diamonds from the deep mantle formed is currently one of the 'hot' topics, since these samples provide one of the only direct means to determine deep mantle chemistry. The proposed experiments have high merit, and will inevitably provide new and interesting data, regardless of the result. One concern, however, is in data interpretation. Throughout the proposal there is an implicit assumption that diamond inclusions provide information on the bulk mantle, but this is not the general consensus. The predominance of eclogitic versus peridotitic diamonds from the transition zone is not automatic evidence that the transition zone is formed from eclogite, but may simply reflect the tendency of diamonds to form in eclogitic environments. This is already demonstrated for diamonds from the lithosphere, where peridotite xenoliths contain only ca. 10% of discovered diamonds. The applicant has a strong background in high-pressure research, and the large experience built up over the years will ensure a high probability of success. The facilities required for the proposed projects are in place, and access to the necessary peripheral equipment appears to be present.

What are the broader impacts of the proposed activity?

The applicant makes a strong case for the continued funding of the split-sphere apparatus at Stony Brook. The facility significantly enhances the infrastructure for high-pressure research, although it is not the only facility in North America that is available. Collaboration of the PI with other scientists will be crucial to maintaining a high accessibility of the facility, and a different funding structure than was previously available through CHiPR may be beneficial. There is sufficient scope within the proposed research projects to enable students at all levels to make a contribution.

Summary Statement

The proposal to measure phase equilibria relating to the formation of deep diamonds is excellent and should receive the highest priority for support. The overall rating was reached using a rating of 75% for intellectual merit and 25% for the broader impacts.

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Review #5
PROPOSAL NO.: 0308362
INSTITUTION: SUNY Stony Brook
NSF PROGRAM: PETROLOGY AND GEOCHEMISTRY
PRINCIPAL INVESTIGATOR: Gasparik, Tibor
TITLE: Experimental Investigation of the Origin of Inclusions in Diamonds From the Deep Mantle
RATING: Very Good

REVIEW:
What is the intellectual merit of the proposed activity?

This is a most unusual proposal that I believe deserves significant discussion by the panel. At the outset I want to make clear that I have never had any interaction with the PI or any of his associates in the Stony Brook Center for High Pressure Research (CHiPR), a 10+ year research initiative that has apparently recently drawn to a close. As such, I hope to be able to offer an objective view, free from preconceived notions about the science or politics of the former initiative, or its apparent successor, the Consortium for Materials Properties Research in Earth Science (COMPRES). But, this same lack of prior interaction with these groups could well leave me ignorant of important prior history, or even current discussions, so I encourage you to interpret my comments with this in mind. Also, although I am an experimental petrologist, my work is exclusively in the piston-cylinder pressure range. Thus, while I have a passing acquaintance with work like the PI's at much higher pressures, I do not profess to be an expert in this particular area. The proposal seems to me to consist of two quite separate components. The first seems almost entirely political and is essentially a plea for the Petrology & Geochemistry program to pick up the funding that was apparently previously provided by Geophysics (during the CHiPR years) to enable phase equilibrium studies to continue, using the ultra-high pressure, multi-anvil facilities in place at SUNY Stony Brook. We are told that the new COMPRES initiative has jettisoned petrological and geochemical studies in favor of an approach exclusively focused on measuring the physical properties of materials thought to be important in the upper 1000 or so kilometers of the mantle. (Although, curiously, the PI states in the first sentence of the third paragraph on p. 2 that the measurement of physical properties of mantle minerals is nearing completion.why the COMPRES initiative, then?). The PI asserts that this focus on geophysical measurements alone, leads to a very unbalanced approach to understanding the constitution of this region of the mantle. Further, he argues that this has led many in the geophysics community to ignore chemical aspects of the problem, and the complexities that could be revealed by phase equilibrium studies, in favor of the simplest models possible that seem consistent with the remote sensing information provided primarily by seismology. He further asserts that when the geophysics community does adopt the view that chemical aspects of the problem might be worth considering, they are content to limit their exploration to the simple (Mg,Fe)2SiO4 chemical system, reasoning that this must be what most of the mantle is made of and thus this is an adequate approximation, with no need to consider other chemical components or the real complexity that must exist. Another interesting assertion that he puts forth is that the U.S. community as a whole views the former efforts of the PI's and others at CHiPR as a near-monopoly on research at these very high pressures in the U.S. and thus no other institutions have ventured into this area of research. To the extent this is true, the PI argues that if Stony Brook gets out of the ultra high pressure phase equilibrium business, then the U.S. will effectively be doing so as a nation. It is true that there are very few facilities in the U.S. able to operate at pressures in this range (Walker's lab at Lamont, Asimow's operation at Caltech, and Agee's new facility at New Mexico come to mind) so there is some truth to this. To bring this discussion of the political aspects to a close let me offer the following obvious observation. Because of the politics inherent in the transition from CHiPR to COMPRES the PI now finds himself unemployed and facing the very real possibility of having to walk away from what I view to have thus far been an very successful, productive, and even pioneering 20+ year career as a research scientist. At the same time though, nobody should ever has projected that CHiPR would go on forever and, with it now disbanded, the question arises as to what the community can or should do to enable the PI to continue making contributions like those he made during the CHiPR years, which I believe to have been very valuable. There is no question in my mind that the PI's abilities, track record, and promise of future significant discoveries are all strong. On the other hand, if every initiative supported by NSF leaves a trail of soft money researchers that need to be fully supported into the indefinite future, an inordinate amount of NSF budgets will soon be by funneled in that direction rather than into funding new initiatives and individual PIs who seek only summer salary. This is a tough one.thus my recommendation at the outset that the panel give this proposal significant discussion. Moving now to the science portion of the proposal I begin by noting that the PI's productivity during his last two grant cycles (an initial grant followed by a renewal for a total of five year's support, I presume) was spectacular. Fully 14 quite different studies were pursued, completed, and presented and published in a timely manner (12 papers in good journals). These studies are detailed on pages 3-7 of the proposal and convince me that the community got an incredible value for the very modest cost of these two grants (<$200K for total for 5 years; ~$40K/year!). I suppose CHiPR paid the PI's salary and that's why these grants were as small as they were but, any way you look at it, a lot of good science was done for not much NSF money. But, is it good science? On reflection I conclude that the answer is yes. Granted, not many of the studies are particularly novel in their design but the fact remains that Gasparik has been probing areas of P-T space of obvious relevance to mantle processes, that nobody has looked at systematically before. When confronted with such a wide open playing field, the obvious, and correct choice of experiments are the simple 'cook and look' type. While these experiments may not sound novel, the do provide first order information that can't be obtained in any other way and that can be built on later.

Proposed Work:

For the future, the PI proposes three quite separate lines of inquiry. The first proposal is to extend his former systematic phase equilibrium studies in the NCMAS system with bulk compositions with assorted pyroxene or olivine stoichiometries by adding Fe. Clearly Fe is an exceedingly important component in the real mantle and I wonder if the absence of Fe in the PI's former work is in part responsible for the geophysicist's apparent lack of use of his results. But, as is true at lower pressures too, Fe is a problem-child when it comes to doing experiments. The PI acknowledges this in stating that the capsule (Re)/furnace (LaCrO3) configuration used in multianvil assemblies leads to oxygen fugacities that are much too high and lead to the bulk of the iron in such experiments being ferric. Having never done this sort of work I'll take the PI's word for this but I wonder if there might be other problems too, such as loss of Fe from the charge to the Re capsule, as occurs when using Pt capsules. The PI proposes to solve this problem by adding Fe to his charges as finely powdered Fe metal which he asserts will 'buffer' the Fe oxidation state to reasonable values so long as Fe metal persists in the experimental charge. While not really a rigorous buffer, this method seems to me to have merit although I note that the charge will oxidize as the experiments run and thus the ferric/ferrous/native Fe ratios will change with time. This is unfortunate but I don't have any better suggestions. While these proposed experiments sound rather routine, it needs to be kept in mind that the P-T conditions at which they will be run are anything but routine. There is no doubt in my mind that these results will be important. The second proposed task is a set of experiments aimed at providing constraints on the origins of mineral inclusions that have been found in diamonds from the deep mantle. The PI has already met with a good deal of success pursuing this line of inquiry (detailed in results of prior support) and it seems that continued studies along these lines will also bear fruit. As the PI states, these inclusions today are typically found as single crystals within diamonds and it is the PI's operating principle that these single crystals were, at their pressure of origin, the multi-phase mantle assemblage appropriate for that depth. With decreasing pressure apparently, a variety of phase transitions and solid state reactions occur, resulting in phases dissolving into one another with the final result being a single phase with what the PI suspects to be the bulk mantle composition at that depth. If this is indeed true that then inclusions are a real gold mine and experimentation on such bulk compositions is a very important undertaking. For me though, this seems like a huge leap of faith and, as the PI details in the final paragraph on p. 12, there are good reasons to be concerned about this presumption. But, the fact remains that the inclusions are representative of something from great depth and are thus worth looking into by experimental means. The final line of inquiry is only sketchily developed and consists of exploratory experiments aimed at eventually including Cr in the PI's systematic phase equilibrium work at very high pressures. The PI points out the important role played by Cr in mantle bulk compositions with high pressure garnets often being Cr-rich and with chromite often appearing as inclusions in diamond. It's difficult to get excited about this work as proposed, but the fact does remain that Cr is important in the mantle so its effects do need to be evaluated at some point.

Technical Aspects

The PI has been a pioneer in developing ultra high-pressure experimental techniques for over 10 years and I am therefore confident that he can do the proposed experiments as well as anybody in his business.

Broader Impacts of the Research

Here the PI points to two principle broader impacts of his past and proposed research. The first is the book he has apparently just published presenting in phase diagram form an internally consistent synthesis of his and others' work at very high pressure. I think a synthesis like this is excellent as it forces the PI to evaluate internal consistency, and the relationships between his many former studies. But, like with all model system work, it will likely never find wide use outside the PI's immediate field because the model systems differ so from real rocks (no Fe or Cr,, for example). Nevertheless, the PI is to be congratulate for pulling together this summary volume. The second obvious 'other' impact of his proposed research is that it would revitalize phase equilibrium studies in the Stony Brook facility, which is used by lots of students, interns, postdocs etc.

SUMMARY RECOMMENDATION

I find this proposal quite troubling for a couple of reasons. First, it is a real shame that the apparent competition between the mineral physicists and the high pressure phase equilibrium researchers has developed when it is so obvious that the correct approach should accommodate multiple lines of inquiry. It is also a shame that the development of this apparent rift came at the same time CHiPR was being disbanded and COMPRES was being assembled and apparently left the PI 'out in the cold'. He is a very talented scientist with lots of good work ahead of him. On the other hand though, I don't see it as NSF's responsibility to pick pieces once a former NSF-funded initiative dissolves. In the end, I think the PI's proposed research has to drive the process, although do appreciate having the political aspects of his situation explained to me since I am not a member of the ultra-high-pressure community. Of the three areas of research that the PI described I think the work on bulk compositions matching the inclusions in diamond (with Fe, and Cr, right?) is the most compelling, followed by the routine phase equilibrium exploratory work with Fe added. The third task is so poorly developed that I recommend dropping it. The bottom line of the budget is staggering ($890K for 3 years) and is a good reminder of how much people cost. I note that ~70% of the total is salary plus OPE plus indirect cost. I also not the that the postdoc is never really justified. In the end, I recommend that every effort be made to fund as much of this proposal as possible. But, the cost is so high that I think compromises have to be made and I recommend eliminating the post-doc and eliminating task three (the Cr work) and with it, year three.

SUMMARY SCORE: VERY GOOD
What are the broader impacts of the proposed activity?
see above
Summary Statement
see above