CHBE 551 Lect 04

1. CHBE 551 Lect 04 Research Planning: Finding A Good Proposal Idea The Heilmeier Criteria

2. Objective For Today • Start to discuss proposals • A proposal is a request for funding for a research project • A research project is a piece of work that • Advances an important field • Will lead to 4+ papers in 2 years

3. Outline Object for today: Learn how to evaluate Research ideas • Deciding if a research problem is good for your career • Choose problems that are the right place on the knowledge curve • Deciding if an idea is fundable • Evaluate ideas based on the Heilmeier criterion and whether a case can be made for a proposal • Can it be done in 2 years with 1-2 graduate students

4. Background: Steps In Proposal Writing • Finding a good idea • Finding an interesting problem • Meets national/company goals • Matches your skills • Fun to do • Literature search • What has been done before • What is your competition doing (look at their proposals/talks) • Identifying a possible funding source • Federal or other • Writing a proposal

5. Good Research Ideas Important To Proposal Success • A proposal starts with an idea about an important problem that if you can succeed in solving, will advance the state-of-knowledge, educate graduate students and make an important impact on society • Have publishable results in 1-2 years • A proposal asks questions, and proposes an approach to answering the questions

6. The Hourglass Picture Of Research Start with an important big question Focus to solvable question Observe Analyze data Reach conclusions Generalize back to big problem Adapted From William M.K. Trochim Cornell

7. Example Big Question: Biofuels (Cellulosic ethanol) presently too expensive. Can we reduce the cost? Wyman Paper: Pretreatment has largest potential for cost reduction Solvable question: Can tethered sulfuric acid (polyelectrolyte brush) be used in place of sulfuric acid to reduce cost? Measure kinetics of polyelectrolyte catalyzed cellulose conversion as a function of polyelectrolyte structure Analyze data Conclusions: kinetics, structural functional relationships Generalize: Economic analysis to determine whether these catalysts reduce the cost of cellulosic ethanol

8. Finding The Solvable Question Key Start with an important big question Focus to solvable question Need to convince reviewers it is solvable Observe Analyze data Limits problems to ones the reviewers think they can solve Reach conclusions Generalize back to big problem Adapted From William M.K. Trochim Cornell

9. What Are The Most Important Questions In Your Area? • Try to work on the most important questions in your area • Be sure to focus on the least publishable unit • Do not overreach • Plan for 4 papers

10. Process For Finding Research Ideas Refine the idea Good enough to get funded? Fits into career plans? Start Find an idea Evaluate the idea The hard part is knowing if you have a good idea that is solvable, fundable and will advance your career

11. How Do You Tell If An Idea Is Good For Your Career? • Evaluating yourself • What are you good at • What do you enjoy • What would sustain your career • Is the problem good for you? • Choose problems that are the right place on the knowledge curve

12. You Also Need To Be At The Right Point On The Knowledge Curve Knowledge Evolves With An S Shape Curve Time to move on Difficulty In Obtaining Grant NSF DOE First Proposal Filling holes in existing work Progress Army Navy NIH Startup Funds 10-20 publications Mining discoveries Discovery 1-5 pubs DARPA Time

13. When You Are Evaluating An Idea It Is Important To Know Where It Is on the Knowledge Curve • Completely new ideas/molecules • Nothing like this published before • Areas/sub areas with 10-20 publications but still significant holes • Areas with 100+ publications that need to be cleaned up Route to fame but high risk before tenure Prime target for beginning investigators Usually people near scientific retirement unless area very important

14. I Like To Have A Mix Of Projects • Projects near top of curve for productivity • Papers in well established areas • Projects near the middle/bottom of the curve for future • Breakout findings = fame • You need to continuously prospect for new curves to explore

15. Also Need To Know If You Have A Fundable Idea Heilmeier Catechism to evaluate ideas According to Heilmeier, every good proposal answers the following questions on the first page • What are you trying to do? Articulate your objectives using absolutely no jargon. • If you cannot explain it simply you are not going to get it funded • Who cares? If you're successful, what difference will it make? • What's new in your approach and why do you think it will be successful? • What special skills do you bring to the question? • How much will it cost, how long will it take and what are the risks? • What are the midterm and final "exams" to check for success? George Heilmeier Head ARPA Pres. Bellcore Inventor of flat panel display

16. Expanded Heilmeier Criteria • What is the problem, why is it hard? • How is it solved today? • What is the new technical idea; why can we succeed now? • What is the impact if successful? • How will the program be organized? • How will intermediate results be generated? • How will you measure progress? • What will it cost • Why should they fund you rather than someone else? Adapted From Gio Wiederhold, Stanford

17. Example From My Own Work In 2005 DARPA had a proposal call for miniature (1 cm3) gas chromatographs Should I respond?

18. Questions I Asked • Can I do it • Will I be able to do it better than anyone else • Will if be rewarding to do? • How does it fit into my career plans?

19. What Could I Do New Fun With Preconcentrators? • Existing purge & trap preconcentrators Goal • Challenges • Small fluidic devices • Better adsorbents

20. Could New Adsorbents Enable Devices? • Existing adsorbant materials • Tenax (discovered 1968) • Activated carbon – first used 1796 • Many new adsorbents • MOF’s • Mesoporous silicon • Nanoposts & nanowires • Applying new materials to an old problem is a good research thrust

21. Masel Expert On Adsorption • 200+ papers • 2 textbooks • Partner (Mark Shannon) expert on fluidic components

22. Interesting Questions For RIM • Could new materials be used? • Presently no practical applications for any of the materials – real applications will be noticed • Materials likely would need modification for application • Fun materials synthesis • Effect of structure on function unknown • Good science issues that will lead to lots of papers • RIM long term research interest

23. Are Heilmeier Criteria Satisfied? • What is problem why is it hard? • Need to adsorb many molecules into a small volume • How is it solved now • Carbon or tenax – insufficient capacity • What is the new technical idea; why can we succeed now? • New materials that did not exist in 1965 • Higher surface area, promising structure • What is the impact if successful? • Shrink purge and trap to chip size (improve sensitivity of a host of analytical devices) • New directions in a standard analytical technique • Why should they fund you rather than someone else? • Unique skillset

24. Project Was Funded & Idea Worked • MOF’s 10-100x better adsorption capacity than Tenax, carbon • Tailor selectivity • Many new discoveries • New frameworks (tailored adsorbents) • New synthesis – much less expensive • Particle size control • Water stability How can I use these accomplishments to break out into new areas? • Drug delivery? (JACS paper) • MRI contrast agents? (JACS paper) • New separation processes (Key Dow Need) Consider these more carefully in lect 4

25. List Of Why Proposals Are Turned Down Class I: Problem (58 percent} • The problem is of insufficient importance or is unlikely to produce any new or useful information. • The proposed research is based on a hypothesis that rests on insufficient evidence, is doubtful, or is unsound. • The problem is more complex than the investigator appears to realize. • The problem has only local significance, or is one of production or control, or otherwise fails to fall sufficiently clearly within the general field of the agency. • The problem is scientifically premature and warrants, at most, only a pilot study. • The research as proposed is overly involved, with too many elements under simultaneous investigation. • The description of the nature of the research and of its significance leaves the proposal nebulous and diffuse and without clear research aim. Source: Ernest M. Allen “Why Are Research Grant Applications Disapproved?” 132, 960 1532-1534.

26. Why Are Proposals Turned Down II Class II: Approach (73 percent) • The proposed tests, or methods, or scientific procedures are unsuited to the stated objective. • The description of the approach is too nebulous, diffuse, and lacking in clarity to permit adequate evaluation. • The over-all design of the study has not been carefully thought out. • The statistical aspects of the approach have not been given sufficient consideration. • The approach lacks scientific imagination. • Controls are either inadequately conceived or inadequately described. • The material the investigator proposes to use is unsuited to the objectives of the study or is difficult to obtain. • The number of observations is unsuitable. • The equipment contemplated is outmoded or otherwise unsuitable.

27. Why Are Proposals Turned Down? III Class III: Investigator (55 percent) • The investigator does not have adequate experience or training, or both, for this research. • The investigator appears to be unfamiliar with recent pertinent literature or methods, or both. • The investigator's previously published work in this field does not inspire confidence. • The investigator proposes to rely too heavily on insufficiently experienced associates. • The investigator is spreading himself too thin; he will be more productive if he concentrates on fewer projects. • The investigator needs more liaison with colleagues in this field or in collateral fields. Class IV: Other (16 percent) • The requirements for equipment or personnel, or both, are unrealistic. • It appears that other responsibilities would prevent devotion of sufficient time and attention to this research. • The institutional setting is unfavorable. • Research grants to the investigator, now in force, are adequate in scope and amount to cover the proposed research

28. An Example Electrochemical CO2 Recycle to Syngas • How is it solved now • CO2 electrolysis in aqueous solution • What is problem why is it hard? • Water reacts at lower potential than CO2 so mainly electrolyze water not CO2 • What is the new technical idea; why can we succeed now? • Use ionic liquids in place of water • New materials that did not exist in 1965 • Very high solubility of CO2 • What is the impact if successful? • Recycled gasoline for less than $2/gal • Why should they fund you rather than someone else? • Unique skillset • Need preliminary data

29. Summary: You Need To Evaluate Proposed Ideas Before You Write The Proposal • Is it good for your career? • Fit your personality, skillset • Fun to do • The right place on the knowledge curve • Can you get 4 papers in two years? • What is the minimum publishable unit? • Is it fundable? • Satisfy Heilmeier criterion • Can you make a case for funding?

30. Questions?