Finding a PhD Topic Kathy Yelick EECS Department, UC Berkeley and Lawrence Berkeley National Laboratory

Who am I? Why CS? –Hooked on the first course Why a PhD? –Feeling of where I fit in Personal: –BS/MS/PhD from MIT –Berkeley Assistant Prof. in 1991 –Married Jim in 1993; Megan in 1996; Nathan in 1998 –Timing: Tenure in 1996, Full Professor in 2001, Joint LBNL Appointment Hobbies: –Skiing, Soccer Mom, (formerly) crew, hiking, biking

Fear of Topic Selection Settling on a PhD topic is often a low point in graduate school –Even for the most successful students Why? Because it is very important! –You’ll work on it for a few years in school –Often will work in the area for years after –Will define your area for your job search But, you can change areas later –The topic is likely to shift along the way

What is a Topic? The difference between a project or area and a topic What is the thesis of the thesis? Base on Five Heilmeier Questions 1. What is the problem you are tackling? 2. What is the current state-of-the-art? 3. What is your key make-a-difference concept or technology? 4. What have you already accomplished? 5. How will you measure success? Acks: –Based on Patterson’s “How to Have a Bad Career…”

What to Consider in Choosing a Topic What kind of job are you interested in? –Top 10, teaching, gov’t lab, industry What are your strengths? –Programming, data analysis, proofs (key insights vs. long/detailed verifications) What drives you? –Technology, puzzles, applications Practical considerations –Does your advisor know anything about it? –Do you (your advisor) have funding for it?

Digression: Advisor’s Perspective The funding rat-race –Your write a grant proposal –You make promises ~3 years out Not too specific, but specific enough… –It gets funded –You hire student A to “work on the grant” –Student takes an interesting left turn –Hire student B to finish the grant work –Write another grant to cover student A

5 Ways to Find a PhD Topic

1) Flash of Brilliance Model You wake up one day with a new insight New approach to solve an important open problem Warnings: –This rarely happens –Even if it does, your advisor may not agree that it’s a great idea

2) The Apprentice Model Your advisor has a list of topics Suggests one (or more!) that you can work on Can save you a lot of time/anxiety Warnings: –Don’t work on something you find boring, fruitless, badly-motivated,… –Topics can be too close to an advisor’s interests

3) The Phoenix Model You work on some projects You think very hard about what you’ve done and are doing to look for insight –Re-implement in a common framework –Identify an algorithm/proof problem inside The topic emerges from your work Especially common in systems (the theory variation is the stapler model) Warnings: –You may be working without “a topic” for a long time

4) The Synthesis Model Read some papers from other fields Look for places to apply insight from another field to your own –E.g., databases to compilers Warnings: –You can spend a career reading papers! –You may not see any useful connections

5) The Expanded Term Paper Model Take a course in your area or in an area that gives you a new perspective –E.g., theory for systems and vice versa Do a project/paper that combines your research area with the course –Low risk topic selection Warnings: –This can distract from your research if you can’t find a related project/paper

What to do when you’re stuck Read papers in your area of interest –Write an annotated bibliography Read a PhD thesis or two Read your advisor’s grant proposal Take a project class with a new perspective Do some non-thesis work for your group –Keep working on something Get feedback and ideas from others –Do an internship

Don’t be Afraid to Take Risks Switching areas can be risky –Move outside your advisor’s area of expertise –Don’t know the related work –Starting from scratch But it can be very refreshing! –Recognize when your project isn’t working –Hard to publish negative results

“Technology And Courage” Ivan Sutherland, 1996 Courage: to perceive risk and proceed in spite of it –Research: high probability that an attempt will fail –If inadequate courage, Work up courage, reduce risk, reduce perception of risk, or don’t do it 1.External Encouragement (rewards and punishment) Deadlines, groups of people, mentors, seminars, tenure, taking / teaching classes, starting companies, stock 2.Self Encouragement Getting started: warm-up project, break into tasks and do 1 st one To continue: refuse to let urgent drive out the important 3.Rewards Thrill of discovery, following curiosity, beauty, simplicity, fun Acks: –From Patterson’s “How to Have a Bad Career…” and –Sutherland’s paper at

It’s Not About the Topic It’s about the area: –Is it important? Timely? Jobs in the area? And the tools: Many researchers have one really good hammer –Use it to solve many problems –More experienced than others at using it –Can be a theoretical technique, a software system, etc.