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CHE 594 Lecture 5. Finding and Idea II. Research Planning Starts With The 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?

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che 594 lecture 5

CHE 594 Lecture 5

Finding and Idea II

research planning starts with the heilmeier criteria
Research Planning Starts With The 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

key steps in research planning
Key Steps in Research Planning
  • Identify an interesting problem
  • Do a literature search to answer the following questions
      • How is it solved today – what is known?
      • What are the holes in the literature
      • Why haven’t those holes been filled?
        • It is insufficiently important (poor proposal topic)
        • No one has gotten to it (OK proposal topic)
        • New technology enables solution (Great proposal topic)
        • You have a unique solution (Great if convincing)
  • Narrow the question down to an achievable goal
      • Usually involves formulating smaller questions or testable hypotheses
  • Find a way to answer the questions
  • Identify intermediate answers (papers)
  • Develop a method to measure progress
  • Find a risk mitigation strategy
the hourglass picture of research
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

example a problem that professor masel is thinking about now
Example A Problem That Professor Masel Is Thinking About Now

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

finding the solvable question key
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

characteristics of a good solvable question
Characteristics Of A Good Solvable Question
  • Clear relation to the big problem
  • Clear reason why to do the work
      • Why hasn’t the work be done before?
        • Insufficiently important (Poor proposal topic)
        • No one has gotten to it (OK proposal topic)
        • New technology enables solution (Great proposal topic)
        • You have a unique skills (Great if convincing)
  • You have the skillset to solve
  • Key results in 1-2 years (for 3 year project)
    • Many publishable intermediate results
  • Lead to follow-on studies
  • Fun to do
typical good solvable problems
Typical Good Solvable Problems
  • Critical test of an important hypothesis
  • Better understanding of the critical variables that underlie an important problem
  • Application of new technology to create new insights to an important problem
  • New solutions to an important problem enabled by new materials new equipment or new insights from other fields
  • Most good proposals apply a new technique to an old problem, or an old technique to a new problem
good science and good proposals not the same
Good Science and Good Proposals Not The Same
  • Good science uses inductive and deductive reasoning

Deductive Inductive

  • NIH encourages hypothesis based (deductive) proposals

Adapted From William M.K. Trochim Cornell

method to tell if problem is solvable
Method To Tell if Problem is Solvable
  • Outline 1-2 papers/yr that you would like to write on a given topic.
    • What is the proposal supposed to measure or calculate?
    • What techniques will you use?
    • How long will it take YOU to set up the experiment and take the data? (students will take twice as long)
  • Assume you are successful (4 papers published in 2 years)
    • If everything works will you have an answer to the question you raised?
    • If parts of the experiment do not work, can you still write papers on the results?
a task table for a muri project

Table 1 Task Summary, Roadmap

A Task Table For a MURI project

Current Status

Issues

Proposed Approaches

Microburners as heat sources

Masel and Shannon already demonstrated that flames can propagate in 100-1000 micron spaces

Need equations for flame stability as a function of geometry, wall composition, wall temperature, fuel, oxidizer, stoichiometric ratio

Measure combustion limits in micron to millimeter scale burners

Develop model of combustion process

Analyze results to produce design correlations, scaling rules

Need equations for heat output as a function of geometry, wall composition, wall temperature, fuel, oxidizer, stoichiometric ratio

Measure conversion, heat output in micron scale burners

Use model to calculate conversion, heat output

Analyze results to produce design correlations, scaling rules

Key properties that determine flame stability have not yet been measured for many candidate wall materials

Measure key wall properties: accommodation coefficients, radical reflectivities of key species

$1,000,000/yr for 5 yr effort

Program managers love this; NSF reviewers hate it, NIH OK

most common mistakes
Most Common Mistakes
  • Writing too ambitious a proposal
    • Proposing too much, too many problems, …
  • Unfocused technical objectives
    • Talking about the large problem instead of a narrower idea that you can really do
  • Not starting early enough
proposal calls as sources of research ideas
Proposal Calls As Sources Of Research Ideas
  • The government publishes many research ideas
    • Broad agency announcements
    • Small business innovation research (SBIR)
  • These are good sources of ideas even if you are not eligible

You can find a list of SBIR programs at

http://www.sba.gov/SBIR/indexprograms2.html

I posted a number of these calls at

http://www.scs.uiuc.edu/~rimclasses/che594/proposal_ideas/

email lists of funding opportunities
Email Lists Of Funding Opportunities
  • NSF: https://service.govdelivery.com/service/multi_subscribe.html?code=USNSF&custom_id=823
  • NIH Guide LISTSERV
  • http://grants.nih.gov/grants/guide/listserv.htm
  • Dept. of Education
  • http://www.ed.gov/news/newsletters/edinfo/index.html
  • Federal Grants
  • http://www.grants.gov/search/subscribeAll.do
be sure to get in touch with the program officer before you submit the proposal
Be Sure To Get In Touch With The Program Officer Before You Submit The Proposal
  • Discuss your ideas
  • Ask questions about format
  • Find out the evaluation criteria, methods
summary you need to evaluate proposed ideas before you write the proposal
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
  • Is it fundable?
    • Satisfy Heilmeier criterion
    • Can you make a case for funding?
list of why proposals are turned down
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?” science 132, 960 1532-1534.