User login


You are here

The incomplete guide to the art of discovery

Zhigang Suo's picture

The warm reception to a previous post on learning to be a PhD advisor reminded me of a book, whose  title now appears as the title of this new post.  The book was written by Jack E. Oliver, a geologist, and was published in 1991 by Columbia University Press.  Looking at the book again the other day, I found the original receipt, dated 19 October 1991, from Chaucer's Bookstore, in Santa Barbara, where I started as an assistant professor at UCSB in 1989.  How delightful! 

Among books and essays that I have read of this kind, Oliver's book is by far most influential in my formative years.  His own career parallels the epoch in geology, during which the plate tectonics was established.  The book is about 200 page long, filled with perceptive remarks and amusing cartoons.  He also provided some background on earth science, which is interesting.  But most his ideas are applicable to any field of research.

I find it hard to encapsulate his ideas in a post, but believe that some of you might benefit from reading this book.   The book is probably out of print by now, but Amazon lists some copies from third-party sellers.  

Here are headings in Chapter 2, Strategy for Discovery:

  • Don't follow the crowd
  • Rebel, but wisely
  • Strive to enhance serendipity
  • Avoid science eddies
  • Study the Earth, and the Science of Geology
  • Seek the nonquestions
  • See your era in long-term perspective
  • Go with intuition
  • Avoid sidetracking trivia
  • Be competitive.  Be a winner.  Be first
  • Argue by analogy
  • Vision, hypothesis, and objective testing
  • The strategy of exploration for understanding

The entry "Avoid science eddies" is particularly illuminating.  It might be fun to make a list of such eddies in our own discipline.  But that will be for another time.

Do you have a book of this kind to tell us about? 


Though not directly related to the art of discovery I've found the book "Why the Professor can't Teach" by the late Prof. Morris Kline quite inspiring.  The book was published in 1977 but a reading today makes it perfectly relevant even today.  An electronic version can be found at .

Even though competitiveness sometimes leads to faster advancement in science, it's not for everyone.   Personally, I would rather do something I find interesting - and hope that it is relevant to the larger world - rather than try to be first in everything I do.   


Temesgen Markos's picture

I read "Why the Professor can't Teach" half a year ago and was surprised how it still makes sense after three decades. So many of the ills he mentioned are still not cured. I liked the author as a result and read more of his work.

"Why Johnny can't Add" is a book on the failure of the "new math" which was embarked on in the west after Sputnik. It concentrates on school math, but is an insightful read. Another author who opposed Prof. Klien's idea wrote a book "Why Johnny can't Prove". I have yet to read that.

Amit Acharya's picture

So what are science eddies? It might help to have a definition for people who are never going to buy Oliver's book. Also, it may help to have your 'fun list' of eddies in mechanics for the mere mortal yet to discover.

Nonequilibrium thermodynamics is one such eddy for sure:)  Most difficult problems can be interpreted as eddies at some stage or the other.  In particle physics quatum gravity might be an eddy.  In my field of expertise, predicting fragmentation and certain aspects of adiabatic shear banding could be classified as eddies too.  The pragmatic thing would be to pick the low hanging fruit but the eddies seem to be more fun.

Zhigang Suo's picture

Dear Amit:

Your first request is easy.  I quote Oliver:

"With a little experience, it is easy to recognize that specialties in science can evolve into a state of increasing isolation.  The practitioners lose touch with the flow and advance of science as a whole yet maintain a whirlpool of activity that consists largely of specialists talking to each other solely about that specialty.  Like an enddy, such groups drift from the mainstream, maintaining an identity for a surprisingly long period.  Eventually, however, and like an eddy, they commonly fade into obscurity."

In short, a science eddy is a specialty in science that is stable for a long time and is isolated from the mainstream of science.

Your second request is tricky for me to respond quickly.  Can we make a list of eddies in mechanics?  Biswajit Banerjee has just nominated a few candidates.  Perhaps we all have our own lists.  It would be indeed fun to talk about them. 

Indeed, if we are not careful, we may as well watch the whole discipline of mechanics elove into a giant eddy.  One might also say that parts of mathematics and physics have long acquired the attributes of eddies.

Oliver continued:

"To avoid being caught in such an eddy, it is important to develop a sufficiently broad perspective of science so that the eddy can be recognized.  It is also important for the scientist working in a specialty to strive continually for interaction with specialists in different fields and with generalists.  And it is vital to maintain a focus on the principal gaols of the science, not just those of a particular specialty.

"This guideline should not be interpreted to mean that a scientist should not specialize.  To the contrary, specialization is almost essential in modern science." 

After a couple of examples of eddies in Earth Science, Oliver concluded this entry with the following paragraph.

"Some readers will challenge the point of this section on the basis that occationally in science a major new development will appear in a subject that otherwise, and to most, seemed devoid of consequence.  Of course, that view is correct.  Discoveries sometimes do come from unexpected places.  But that fact is not sufficent justification for laboring on and on in a field that shows none of the characteristics of a subject ready to produce something important, characteristics such as,  for example, an abundance of poorly understodd observations of a feature of obvious importance.  A certain amount of drudgery is often the key to success in science, but it is not a guarantee to success, and the message of this section is that scientists must continally reevaluate their positions to ensure that their efforts are in a field with promise." 

Amit Acharya's picture

Dear Zhigang,

Thanks for your effort in putting up the qotes from Oliver's book. Indeed, what Oliver calls a scientific eddy is a keen observation although I would have liked it if he had called it something other than an eddy as eddies in turbulence, superconductivity and our very own plasticity (i.e. dislocations) do tend to interact very strongly.

From that last paragraph you added later, however, I am a little confused at his premise of what fields might constitute a scientific eddy. It is hard for me to imagine a stable specialty in science that can be a "subject that otherwise, and to most, seem[s] devoid of consequence." While specialists in scientific fields may be many things, the one thing one cannot hold against them is being ill-informed and, to use a colloquialism, stupid to the extent of going after inconsequential things. To the contrary, it is mostly the smartest people who get into a stable specialty to go after some of the most challenging problems science has to offer.

This brings me to my thesis for this post: perhaps the best way to discover something significant, if one is lucky enough, or to simply enjoy the ride of trying to do so is to NOT avoid scientific eddies by Oliver's definition, but to seek them out and then try to break any isolationism that has arisen, in order to solve the major problems that remain in the  stable, and hence consequential, specialty one is interested in. This has the advantage that by merely getting up to speed with the specialty one has to learn a lot as the masters have worked in the area and anything simple worth picking is necessarily gone. Thus the problems that remain are of a deep nature which more often than not require fresh input from what is not contained within the field to solve them - we all know Einstein had to learn differential geometry to go after general relativity. We should not also forget that he was working on gravity which could be called a 'scientific eddy' in 1900-1915. Reading David Gross's Nobel prize address

also gives a good sense of another perceived eddy that gave rise to pehnomenal discovery (I must say, however, that Gross really went down in my esteem when he made a downright silly comment about engineers/physicists in his Buhl lecture at CMU - something to the effect that physicists are those who have had to study Jackson's Electrodynamics, and apparently this got rid of all the engineers. I don't know what engineers Gross studies with or taught and I am sure poor physicists are just as easy to find as poor engineers. If only Gross really knew what the good continuum mechanics person has to study and the problems (s)he has to deal with!)

Returning to the subject of scientifc eddies, the " isolation" part of the definition begs the question: why does isolationism arise in stable specialties of science? My guesses are the following:

1) There may be a perception of isolation. After all, a stable specialty requires a fair bit of training and very hard work to even get to understand what the essential problems and the methods used for tackling them are, in order to improve on them. So for example, quantum gravity sees a lot of interplay from algebraic geometry. Perhaps a lot of PDE theory as practiced by analysts should feed in too, but at any rate to the outsider none of this may seem familiar and since the problems are really hard, there are no daily promises of an 'elevator to the moon made of carbon nanotubes' being offered, it might seem like all the specialists do is sit and chat amongst themselves.

2) There may be real isolation because the specialists in the field may be willing to solve the problems in their field using tools that they know have been tremendously successful and then the coomon person in the field may think that any new tool is unnecessary. If there are remaining problems in a stable specialty, it must be because a fresh idea, often requiring new tools are required (anything, even the hardest problems, that can be solved with well developed tools within the specialty would have been taken care of by the experts!). For example, because of tremendous successes with elliptic problems in solid mechanics, we try to fit in most new/unexplained phenomena within the framework of elliptic problems or their ill-posed cousins - but may be not all phenomena in solids, ranging from the very old to the very new and all of practical consequence, are supposed to fit here. Another example that Pradeep and I have discussed lately is the paper by Hohenberg and Cross on pattern formation in a volume no less than "Reviews of Modern Physics" - they start by talking about the Navier Stokes equations and Rayleigh Benard convection etc. but then solve scalar PDE without so much as a word about the difficulties of dealing with systems of advection dominated PDE, which is qualitatively different from dealing with a scalar equation even of the same type.

All this said, it is not difficult to see that the pursuit of discovery in scientifc eddies, transcending any isolationism that may be involved, cannot be an easy, comfortable life, both professionally and personally. However, the rewards of the journey are perhaps well worth it.

Finally: a recommendation on an article on how to do research - John Willis's Timoshenko lecture is very insightful (and enjoyable - e.g. - to the effect of 'it is a good idea to write less than one reads' )

Dear Amit, others,

1. Classical electrodynamics *is* bad enough, but continuum mechanics (i.e. mechanics of tensor stress/strain fields) is worse---I mean, by way of difficulty. The reason physicists talk about electrodynamics but not continuum mechanics is because they are taught the former but not the latter---at least, not to a sufficient width (including, say, plasticity) or depth (e.g. the analytic theory of stress analysis).

About physicists attempting to put down engineers: It is helpful to remember the observation that David Hilbert offered: "Physics is much too hard for physicists."

2. My first reaction was that science eddies do exist---as an undesirable thing. People do seem to keep revolving around the same matter even when hardly anything new is resulting out of their "research" activities (or publications). They do seem to work in isolation of not only other researches but even of *reality*. It oftentimes seems as if people do not make deliberate attempts to include all the due complexities of the actual physical phenomena, but prefer to deal with only a subset of them. 

3. In the cases where the isolation does not exist but only is perceived to be so, the remedy is to trace the hierarchical roots of the relevant concepts. If this is not possible (say, because people are so confused about what is fundamental and what is derivative in the first place), then, at least, they could establish the interrelation of the main concepts to the other known concepts via concept maps.

Zhigang Suo's picture

Dear Amit:

I've been thinking about your comments, and believe that I agree with you. Like all analogies, a scientific eddy does not have a one-to-one correspondence of all attributes to an eddy in a stream. We may as well understand a scientific eddy as a specialty in science that is stable for a long time and is isolated from the mainstream of science. With this definition of a scientific eddy, as you have discussed, indeed there might be good reasons for an individual to enter an isolated specialty, reconnect the specialty to the mainstream, and make a significant contribution.

For an individual already in the eddy, however, there might be good reasons to leave.

In either case, an individual wish to evaluate a specialty in a broad context beyond the specialty, and decide whether to enter or leave the specialty according to the evaluation. I should have quoted a sentence from Oliver's book to this effect.

Have a good weekend.

Amit Acharya's picture

Hi Zhigang - In complete agreeement with what you have stated above, especially that first sentence of the last para of your post. best, Amit

T.A.Abinandanan's picture

One of my favourites is the speech by Richard Hamming titled "You and Your Research."

It's available online.

Many thanks, Mr. Abinandanan. The speech you recommended is indeed great! I spent the whole Sunday morning to read throught the speech and found lots of useful information. I probably will print it out and read it again. I sent both the link for the speech and the imechanica website to my friends and strongly recommended them to  read them.

Just a few days back I also read Sukumar's recommendation of Hamming's article. I knew the article even before his posting appeared, and though there are many good things in Hamming's article, I think it is overrated.

Didn't reading through Hamming's article ever generate a sense in you that this article was not so much concerned about articulating the activities of that kind of mind which is dedicated to ever-expanding its own grasp of *reality* (and taking the world along in progress as a result too), but, rather, it was only concerned about a smart corporate ladder-climber sort of guy who, nevertheless, is honest and has sufficient gravitas in his bearing---someone who may be just an average researcher but who does keep trying hard, and keeps a sufficient deference to his employers and superiors.

BTW, Hamming's contributions to signal processing (in communications) are certainly well known. They certainly are good enough that we could take something out of his lecture. Yet, IMHO, Hamming never on his own did a very fundamental (or a very consequential) sort of work. (In his assessment of his own work, when he says things to this effect, he is being realistic, not shy or modest.) By way of comparison to other researchers from his own field, consider, for example, his colleague Shannon (the min. sampling frequency theorem). Or, say, Morlet (wavelets).

A similar difference (of observations being not fundamental or acute enough) permeates through Hamming's thoughts on how to do good research as well, including its motivation. He therefore remains unconvincing when, in passing, he comes to assert a mistaken correlation between the fundamental discoveries in physics (esp. QM) and the young-ness of the age of discoverers. (Contrary to the popular opinion the correlation does not hold beyond approx 35-40%, i.e. it does not hold in 60-65% cases.) ... Talking of young minds in science, contrast, for example, Ayn Rand's idea of scientists: in particular, the hero of the novellete "Anthem," vs. Hamming's idea of a researcher. The contrast is too glaring to require further explanation.

Aaron Goh's picture

On a different axis, I find Stephen Covey's books on effectiveness rather useful.  The Covey name is probably more familiar in industry than in academy.



Arun K. Subramaniyan's picture

A free online version of the book (The incomplete guide to the art of discovery) can be downloaded here. It was released as a part of the open access initiative at the Internet-First University Press from Cornell. One can also order a printed copy from them. 

Subscribe to Comments for "The incomplete guide to the art of discovery"

Recent comments

More comments


Subscribe to Syndicate