How to do a PhD

These curves are marketing material for an "advisory firm". Nothing more, nothing less. The idea of the curbe is more important that the particular points, and the points are often mis-placed. Also, lots of technologies jump around randomly on the curve or move rapidly through some parts, etc.

If you get the first one wrong the rest of the list will not matter at all. The most important questions are, who will my advisor be? What is the completion rate for graduate students under their care? What kind of personal network does the advisor maintain and what kinds of roles do the graduating PhDs go into?

I wish I had known to ask that sort of thing. My advisor typically kept a lab of a dozen postdocs and a single PhD at any given time. I think in 25 years of being a research professor with sizeable grants that advisor only graduated 4 doctoral students, and a rather distressing proportion of the postdocs left not only academia but science after that lab.

I would also try to hang out with the current doctoral students and assess their psychological well-being.

While this is completely valid advice, it might not be applicable with junior faculty who may not have graduated many students. I chose my advisor (who was as assistant professor at the time) based on the belief that I'll get to publish aggressively since it's in both of our interests. But I had no way of knowing how hard it would be to work with her. And I wasn't the only person who felt this way; I saw my fellow group mates (all of us joined the group at around the same time) and other collaborators express similar sentiments in course of time. But since I'd already sunk in time, I decided to stick around.

I was able to successfully complete my PhD, but I took more time than expected. Moreover, I was no way near as productive as I'd hoped to.

I've seen a lot of really good people get very badly hurt pursuing a Ph.D. I did get a STEM field Ph.D. but didn't get hurt.

For a good and broad view of the problem, buried in D. Knuth's The TeXBook is

"The traditional way is to put off all creative aspects until the last part of graduate school. For seventeen or more years, a student is taught examsmanship, then suddenly after passing enough exams in graduate school he's told to do something original."

Yes, here Knuth identifies a significant challenge.

Compared with the OP, here's a very different and much more specific approach that clearly makes a lot of sense and that worked well for me:

First, note carefully that for some work that can be called research the usual, nearly universal criteria are that the work be "new, correct, and significant". Below, keep these three in mind.

Second, get a major in math, at least a good undergraduate major in pure and applied math and hopefully enough more in pure and applied math for roughly a Master's in math. Even if you don't care about the Master's degree, I do very much recommend getting the math for a Master's degree.

Why pure math? The pure math gives you the crucial, central, foundational tools of math, that is, many crucial prerequisites and, broadly, the ability to state and prove theorems. E.g., you will learn how to write math, and that alone will start to put you ahead, even of some high end professors.

What pure math? For your research likely mostly you will use the part of math called analysis but in your studies for more you will also want at least the basics of abstract algebra and maybe differential geometry, combinatorics, and maybe even some in foundations. In addition, if you have some reason to believe you can get some value from algebraic topology or geometry, then, sure study those.

Why applied math? Likely applied math will be closer to the math you will use for your research. What applied math? Sure, e.g., statistics, numerical linear algebra, ordinary differential equations, more in numerical techniques, optimization, stochastic processes, etc.

Third, get your Ph.D. in some field of engineering -- computer science, electronic engineering, mechanical engineering, civil engineering, operations research, statistics, etc.

Three biggie points:

(1) In science and engineering, by far the most highly respected research is that which mathematizes the field. Good work here can help meet the criterion of "significant".

(2) Work in math, well supported with theorems and proofs, is much more difficult to criticize than work that is mostly just experimental or empirical. Good work here can be help meet the criterion of "correct".

(3) The standard and severe weakness of the backgrounds of researchers in most of science and in engineering is way too little in math. Thus, there are a lot of good research problems they can't address. So, your good work here can be help meet the criterion of "new".

So, with your background in math, on (1)-(3) you will have at least a good -- maybe even an overwhelmingly strong -- comparative, competitive advantage.

Another point if you care: Unless your family wants to donate $10+ million or so, it is just super tough to get into an Ivy League university. But getting in as a grad student is much easier -- e.g., I got accepted to Cornell, Brown, and Princeton.

So, you should intend that your research be essentially math for that field of engineering. Usually you will aim to use your math tools to solve a relatively practical problem in that field of engineering, but you might use your math to add to the basic theory of that field; for some wild guesses, you might do something in the theory of predators and prey in environmental engineering; maybe you would have been the one who did Kalman filtering in electronic engineering; maybe in mechanical engineering and continuum mechanics you will make some nice theoretical contribution to materials science.

Why engineering instead of pure math or physical science? (1) Engineering has no end of practical problems -- say, from outside of, and neglected by, academics -- to be solved. So, if you pick, attack, and solve a problem important in practice, then there is a good chance your work will meet the criterion of "new", since the work is mathematical, "correct", and since the problem was important in practice, "significant". (2) In pure math and physical science, the range of candidate problems is much more narrow, e.g., in physics you can try to say what dark energy is -- lots of luck doing that.

So, right, for a research problem in some field of engineering, maybe pick a practical problem that is considered important and that you found someplace, maybe outside academics, maybe on a job, maybe a real job or maybe just a summer job or an internship. I did that: I picked a problem I found at FedEx.

Then, it will be quite good for you to have the problem in mind when go for your Ph.D. I had the problem and a good, first-cut, intuitive solution (worked out on an airplane flight) before I entered my Ph.D. program. In my first year, I took some advanced, relatively pure, not often taught, graduate math coursework that gave me good math prerequisites to let me convert my intuitive solution a solid math solution. So, in my first summer, in six weeks, independently, alone in the library, I worked out the math, with theorems and proofs, and walked out with a 50 page manuscript that was the original research for my Ph.D. dissertation. I recommend doing such a thing.

Getting into research early is commonly considered good advice: E.g., IIRC, the Princeton math department has said on their Web site that a student should have some research underway in their first year. Even, better, have the core research done before the second year -- which is what I did and, I believe, a strong advantage in getting the Ph.D.

The math gave me another advantage: In a course, a problem was apparent -- a tricky, deep question about the Kuhn-Tucker conditions. There was no answer in the course, and I could find no answer in the library. So, I attacked the problem -- the key was some pure math I had -- and found a surprisingly nice solution, in two weeks. I wrote up my solution and got credit for a reading course. But the work was publishable -- presto, bingo, at that university the criteria for a Ph.D. dissertation was that the work be "an original contribution to knowledge worthy of publication". Well, the best way to show that some work is "worthy of publication" is to submit it for publication and have it accepted. I did that. So, technically that work was enough for my Ph.D. dissertation, a second one.

For that problem in the Kuhn-Tucker conditions and for my dissertation research, I never had any real faculty direction. I recommend: Don't wait for the faculty to provide a good problem or direction. Instead, on your own as much as you can, at least if it is easy for you, and it was for me, pick a good problem, do the research, get the work ready for publication, and, hopefully, publish it. For a graduate student to have, early on, from largely independent effort, some work worthy of publication makes essentially everything else in the Ph.D. program and the start of a career much easier and better.

Okay, how to do the research? Well, for me, the core, hard work of the research was a little more involved but, really, not much more difficult than the more difficult exercises in standard, advanced pure math texts.

The difference was, for research, in part need to keep in mind some view from higher up, say, 50,000 feet down to 1000 feet and don't always be crawling around on the ground with the lowest level details (which is common and usually effective enough in solving exercises).

Next, guess: To find and prove a new result, first have to guess it. Sure, make educated guesses based on your solid background but also work just intuitively. So build intuitive models and, as you learn more, revise the models to make them more accurate.

E.g., during the work, is A true? Well, it doesn't seem wrong right away intuitively. But, if A is true, then, hmm, B is true. Could B be true? At least, first-cut, intuitively, naw, not a chance (this may be wrong, but let that happen for now). So, likely A is not true.

You can do a lot of this in your head without writing anything. And, even if slowly, you will learn to do at least some derivations in your head.

Now, for C, intuitively it looks true. So, try to prove C. Gee, the proof doesn't work. Then observe: The proof doesn't make good use of all the hypotheses of C; so, you've been trying to prove something more general than C and likely not true. Bummer. So look again at the hypotheses of C and try to see how they are essential and how to exploit them.

So, continue in this way, maintaining a good view from above the ground level, with lots of intuition and guessing and trying to prove some little things.

When you get a proof of a result that looks good, then write it up, carefully, cleanly, put a date and title on the first page, put a staple in the UL corner of the sheets, and toss it on a stack, continue on, maybe building on what you have.

There is also Polya, How to Solve It.

From A. Wiles, the guy who solved Fermat's last theorem and just won the Abel Prize, is

"Perhaps I could best describe my experience of doing mathematics in terms of entering a dark mansion. You go into the first room and it's dark, completely dark. You stumble around, bumping into the furniture. Gradually, you learn where each piece of furniture is. And finally, after six months or so, you find the light switch and turn it on. Suddenly it's all illuminated and you can see exactly where you were. Then you go into the next dark room ..."

Thanks for taking the time to write this. I found it inspiring to hear a rare positive experience of doctoral education. Your advice about studying math but researching engineering was insightful.