Transcript Research Planning

CHBE Orientation Program
Research Planning
The Heilmeier Criteria
1
Background

Oral Quals in April



Need to identify a piece of work
What are you doing?
Why are you doing it?
2
Outline
Object for today: Learn how to evaluate
Research ideas
 How do you find good research projects


Tackling problems that are the right place on
the knowledge curve
How to sell the project

Evaluate ideas based on the Heilmeier criterion
3
It Is Important For You To Take
Charge Of Your Career

Acquire the skills to meet your career
objectives including:





Technical skills
People skills
Communication skills
Mentors
It is your job to make sure that you
acquire these skills in grad school
4
Key Tasks For Your First Year



Take most required classes
Pass Qual
Start research


Read the literature
Take some data or do some calculations
before your orals
5
Key Objectives For Your Second
Year In Graduate School


Learn how to do state of the art experiments
and/or calculations (Key job in your first two
years of grad school)
Learn how to evaluate your own work. What is
good, what are the weaknesses


Learning what you are good at and enjoy



Become your own worst critic
How do your skills compare to others in the field
Learn what leaders in your field are doing and
how you might contribute
Start to develop mentors

Not just your advisor
6
Background: Key Steps In Research
Planning

Finding a good idea


Finding an interesting problem
 Meets national/company goals
 Allows you to develop your
skillss
 Fun to do
Literature search


What has been done before
What is your competition doing
(look at their proposals/talks)
7
The Knowledge Curve
Knowledge Evolves With An S Shape Curve
Progress
Time to move on
Filling holes in
existing work
Mining discoveries
Discovery
10-20
publications
1-5 pubs
Time
8
Planning Research
Knowledge Evolves With An S Shape Curve
Progress
Time to move on
Start here
Develop Skills
Work Down
Filling holes in
existing work
Mining discoveries
Discovery
10-20
publications
1-5 pubs
Time
9
Matching A Project To Your
Career path

Starting graduate student


Senior graduate student


Choose a project that allows you to develop
skills: How to do experiments, write them up …
Need a project that allows you to develop
independence to carry out a project
Postdoc

Project needs to provide you the opportunity to
plan a research project, direct graduate
students, develop mentors, fans
10
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
11
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
12
Finding The Solvable Question
Key
Start with an important big question
Focus to solvable question
Observe
Analyze data
Reach conclusions
Generalize back to big problem
Need to convince
reviewers it is
solvable
Limits problems
to ones the
reviewers think
they can solve
Adapted From William M.K. Trochim Cornell
13
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
14
Also Need To Know If You Are Working
On Something That Makes impact
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
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
15
Expanded Heilmeier Criteria










What is the problem, why is it hard?
How is it solved today?
Who are the leaders, what are they doing?
What is the new technical idea; why can we
succeed now?
What is the impact if successful?
How will the work be organized?
How will intermediate results be generated?
How will you measure progress?
What will it cost
Why should you do this rather than someone
else?
Adapted From Gio Wiederhold, Stanford
16
Example From My Own Work
In 2005 DARPA had a proposal call for
miniature (1 cm3) gas chromatographs
Preconcentrator
collects the analyte
and injects it in a
narrow pulse
MEMS Pump
Column separates
analyte from
interferents
COTS Mote
Thermal Isolation
Should I respond?
Parallel Detectors
selectively detect
analyte
17
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?
18
What Could I Do New Fun With
Preconcentrators?

Existing purge & trap preconcentrators
Goal
•Challenges
•Small fluidic devices
•Better adsorbents
19
Could New Adsorbents Enable
Devices?

Existing adsorbant materials



Many new adsorbents




Tenax (discovered 1968)
Activated carbon – first used
1796
MOF’s
Mesoporous silicon
Nanoposts & nanowires
Applying new materials to an
old problem is a good research
thrust
20
Masel Expert On Adsorption



200+ papers
2 textbooks
Partner (Mark Shannon) expert on fluidic
components
21
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
22
Are Heilmeier Criteria Satisfied?

What is problem why is it hard?


How is it solved now


Need to adsorb many molecules into a small volume
Carbon or tenax – insufficient capacity
What is the new technical idea; why can we succeed
now?

New materials that did not exist in 1965


What is the impact if successful?



Higher surface area, promising structure
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
23
An Example Electrochemical CO2
Recycle to Syngas

How is it solved now


What is problem why is it hard?


CO2 electrolysis in aqueous solution
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


What is the impact if successful?


Very high solubility of CO2
Recycled gasoline for less than $2/gal
Why should they fund you rather than someone else?


Unique skillset
Need preliminary data
24
Summary: You Need To Evaluate Proposed
Ideas Before You Write The Proposal

Is it good for your career?




Can you get 4 papers in two years?


Fit your personality, skillset
Fun to do
The right place on the knowledge curve
What is the minimum publishable unit?
Is it fundable?


Satisfy Heilmeier criterion
Can you make a case for funding?
25
Questions?
26