It Takes Guts To Do Research



Or rather to find bold paths when opportunity gives only part of a map



Robert Oppenheimer was one of the great physicists of the last century. He is most famous, of course, for his leadership of the Manhattan Project—the project that created the first atomic bomb.

Today I want to talk about research and why it requires a certain amount of courage, a certain amount of nerve, or just plain “guts.”

I am currently reading the book Robert Oppenheimer: A Life Inside The Center by Ray Monk. It was a Father’s Day gift from my dear wife, and I found time to start reading it this weekend. The book is over 800 pages.

It starts a bit slow, but eventually is a pretty good read. The author loves details, so if you read it be prepared for minute bits of information about Oppenheimer. The book could have used, in my opinion, one more edit: several sentences are repeated exactly. I guess a good sentence is hard to write, but using it more than once is annoying. Anyway it is an interesting take on this part of history.

One piece of information is a comment by the author on Oppenheimer’s famous quote after seeing the test of the first atomic bomb. He is quoted as saying:

Now I am become death, the destroyer of worlds

This quote was from the Hindu scripture, the Bhagavad Gita. It is however not the usual translation. Oppenheimer translates a Sanskrit word to “death” that is usually translated as “time.”

Research and Guts

Oppenheimer was unique: brilliant by all accounts, a great leader, yet naive in many ways. Whether we should be happy that he helped create the first atom bombs is unclear. The world might be better if they did not exist, or it might be worse. I will leave that debate for others.

What I learned from the book, especially the first half, is that Oppenheimer for all his brilliance missed many discoveries that could have easily yielded him a Nobel Prize in Physics. He was doing his initial research during the boom times in the 1920’s. The field of quantum mechanics was being discovered by many who did win Nobels. Yet Oppenheimer missed several chances to capture one.

For instance, Harold Urey, whose career path also led to the atomic bomb project, co-authored with Arthur Ruark one of the first English textbooks on quantum mechanics, and went on to discover deuterium, for which he won his Nobel Prize, and produce heavy water. He made the leap to look for deuterium even before the official discovery of the neutron in 1932. Carl Anderson understood and jumped on Paul Dirac’s prediction of the positron in 1932, knowing to look for its traces in cosmic rays, and won his Nobel in 1936, the same year he also discovered the muon.

The question that arises is, why did Oppenheimer miss? The short answer is that he lacked some ability to take the leap, to take the chance, to have the guts to believe in his own research. I will shortly give a series of examples of findings that he could have made and almost did make.

I think there is an important lesson for all of us here. We need sometimes to just believe in what we are doing. Without this conviction we may miss breakthroughs, without this assurance in our ideas we may miss the “big” insight.

Some Examples From Oppenheimer

In the spring of 1930 Oppenheimer published a paper “On the Theory of Electrons and Protons” as a letter to the editor in Physical Review. In the letter, Oppenheimer showed that an earlier paper of Dirac about “holes” had to be wrong. He showed that Dirac’s belief that these holes were due to protons was way off. The holes had to be filled with particles of the mass of an electron, not the mass of a proton which is about 2,000 times larger.

Thus Oppenheimer really had proved the necessity of the positron. Yet Oppenheimer failed to make this claim. Rather he believed that this showed that Dirac basic equation, and hence his whole theory, was wrong.

Dirac continued to argue that these “holes” were real particles. And when the existence of positrons was confirmed by Anderson’s experiments, Dirac shared the credit and the glory.

Oppenheimer with Milton Plesset wrote in 1933 another paper entitled “On the Production of Positive Electrons,” again as a letter to Physical Review. They used Dirac’s theory to calculate the frequency of pair production. But again they claimed it only works for low enough energies. Again Oppenheimer believed that Dirac theory was lacking at high enough energies. Abraham Pais describes this as a “fundamental observation,” which would later be studied as showering—and prove to be of great importance.

Oppenheimer with Wendell Furry worked later on a new extension of Dirac’s theory for electrodynamics. Dirac himself had no response to this new long paper. Later in 1934 Oppenheimer got Dirac to visit him at Caltech. There he persuaded Dirac to listen to a fifteen minute presentation by graduate students on the paper, giving the first attempt to deal with cancelable infinities in quantum field theory by a process later formalized as renormalization. After the presentation the students braced themselves for tough questions from the famous Dirac. He asked only one:

Where is the post office?

One of the graduate students, Robert Serber, obligingly drove him there, and tried asking again for comments. He was cut down by Dirac’s reply,

I cannot do two things at once.

Although renormalization is now recognized as having roots in papers Serber would write a few years later, the larger point is that Oppenheimer and his group missed a chance to energize quantum field theory before World War II. To be sure, the underlying mathematics is so famously abstruse that Dirac himself doubted it as late as 1975, saying:

I must say that I am very dissatisfied with the situation, because this so-called ‘good theory’ does involve neglecting infinities which appear in its equations, neglecting them in an arbitrary way. This is just not sensible mathematics. Sensible mathematics involves neglecting a quantity when it is small—not neglecting it just because it is infinitely great and you do not want it!

Among the first of a younger generation to put renormalization on a firm footing was Kenneth Wilson, who passed away just last week. He strikingly connected the abstract idea of the renormalization group to demonstrable properties of phase transitions in macroscopic materials, and won the Nobel for this in 1982.

Can We Learn From Why?

Isidor Rabi wrote about “why men of Oppenheimer’s gifts do not discover everything worth discovering.” As quoted in the biography of Oppenheimer by Abraham Pais, Rabi noted that “Oppenheimer worked diligently,” “was very often on the track of the solutions,” had impeccable “taste in the selection of the questions,”—“and yet as in the case of quantum electrodynamics the definite solutions came from others.” Rabi first pinned it on Oppenheimer’s immersion in Eastern mysticism, but went on to say something more applicable:

He was insufficiently confident of the power of the intellectual tools he already possessed and did not drive his thought to the very end because he felt instinctively that new ideas and new methods were necessary to go further than he and his students had already gone. Some may call it a lack of faith, but in my opinion it was more a turning away from the hard, crude methods of theoretical physics into a mystical realm of broad intuition.

I think we can learn a lot upon replacing “physics” by “computer science” in this quotation. Well perhaps it is best for me to ask you, the readers, for possible examples.

Open Problems

Perhaps some of you can share an example of your own.

[Wendell Fuzzy–>Furry, other format tweaks]