Advice for a Young Scientist

My career has included astrophysics and space physics, always with a theoretical emphasis. My first papers calculated nuclear reaction rates in dense stars, particularly neutron stars, but I branched out to other areas or theoretical astrophysics. However, most of my work was in the plasma physics of the magnetosphere and ionosphere of the Earth. The central theme of my work in space physics is the Rice Convection Model (RCM). This paper very briefly describes the development of the RCM, which involved many colleagues over the course of more than 50 years, in which our understanding of magnetospheric physics advanced dramatically. However, this present paper is not organized in terms of a chronicle of technical advances. It is organized in terms of what I think I learned in my career.


Perspectives of Earth and Space Scientists
WOLF 10.1029/2022CN000177 2 of 7 I should remark at the beginning that my thesis concerned nuclear reactions in stars, which had nothing to do with space plasma physics.However, I was a Caltech graduate student in the early 60s, which was in the early days of the space program, and the Caltech Jet Propulsion Laboratory was receiving data from early Mariner flights out into the solar system.There was also one Caltech professor who did research in space plasmas.So the net result is that I occasionally attended a seminar in space plasma physics.
The first talk I ever heard about space physics was from an old Caltech professor named Leverett Davis, who showed data from some Mariner spacecraft that had ventured out into the solar wind.He showed line plots of magnetic field components, velocity components, density, etc. versus time.His slides that were pretty standard in space plasma physics: curves with lots of bumps and wiggles, sometimes without much obvious meaning.In a physics department we were used to seeing comparisons of data with theory, but Professor Davis did not show any of those.Robert Christy was a physics professor in those days.He was a tall, slow-talking, dignified Lincolnesque character, and he chaired the weekly physics seminars.He always sat in the front row and had a habit of asking penetrating questions.He asked Professor Davis about the possibility of getting more direct comparisons with theory in the area of space plasma physics.Davis mumbled something about how difficult that was.The answer was not illuminating, but the question stuck in my mind as a central challenge for physics in the space age.As it turned out, I wound up devoting much of my career trying to develop computer models that could be compared with space plasma data.I also remember Sidney Chapman giving an astrophysics seminar at Caltech.Of course, he was one of the founding fathers of magnetospheric physics.I remember him as a short, very old man with an English accent and a black suit.Anyhow, that seminar gave me my first introduction to the idea of a magnetosphere, the idea that the Earth's magnetic field could carve out a cavity in the solar wind.Chapman essentially presented the Chapman-Ferraro theory of the magnetopause (Chapman & Ferraro, 1930, 1931).This was my introduction to magnetospheric theory, so I certainly got introduced to the subject by the right guy.Chapman was a wonderful mathematical physicist-very good at formulating elegant mathematical idealizations that captured the essence of plasma processes in space.I remember that seminar being very interesting and going back to my office and arguing with my astrophysicist officemate about whether Chapman's argument could possibly be right.
After I got my degree and started looking for a job, I decided I wanted to do something different than nuclear reactions in stars.By chance, I got an opportunity for a job in a group at Bell Labs that did space plasma physics.Nobody knew much of anything about the subject at that point, so they were willing to pay me to learn the subject and start to do research in it.But because of attending those two seminars at Caltech, I already had an interest in the subject.If I had not attended those seminars, I probably wouldn't have chosen a career in space plasma physics.
Let me mention another seminar that made a lasting impression, in a more minor way.The speaker was a Caltech professor, a very senior low-temperature experimentalist, though I fortunately cannot remember his name.He was talking about some phenomenon he had observed in the lab.To explain it theoretically, he started by writing down a fairly simple equation.Professor Christy objected that the two sides of the equation had different units.The speaker stared at the blackboard for a minute and had to agree that the units were wrong.But he asked the audience to ignore that temporarily and let him proceed with his argument, which was intended to be the rest of his talk.Christy commented that if a formula is nonsense, then anything that follows from it is going to be nonsense.That not particularly diplomatic remark destroyed the guy's seminar.What I learned from that to always check units when you are doing paper-and-pencil calculations.

Do Not Take Professors Too Seriously
My thesis advisor at Caltech was John Bahcall.He eventually became one of the most famous and influential astrophysicists of the late twentieth century, but he wasn't famous when he was my advisor.He was a postdoc when I first started working for him and eventually got promoted to assistant professor.
Caltech had a theoretical seminar every week, where theorists from different areas of physics would give presentations.Bahcall gave a theoretical seminar about part of my thesis work, which had to do with calculating the rate of neutrino emission from a neutron star.That involves a weak interaction, where a neutron beta decays into a proton, electron and antineutrino, but it can only happen while the neutron is getting hit by another neutron.The most interesting result of our calculation was that the reaction rate was proportional to the eighth power 10.1029/2022CN000177 3 of 7 of the temperature (Bahcall & Wolf, 1965).Bahcall finished the presentation, and Feynman stood up and said that our results, and particularly the eighth power, could not possibly be right.Feynman was never wish-washy.Then Murray Gell-Mann got up and said that what was needed was less calculating and more thinking.He was obviously mad and stomped out.I had no idea what he was mad about.However, Gell-Mann was the second most famous professor in the department and had the reputation among the graduate students as being smarter than Feynman.Actually, both Feynman and Gell-Mann received Nobel prizes a few years after this, Feynman for development of quantum electrodynamics and Gell-Mann for inventing quarks and developing a systematic group-theoretic way of looking at particle physics.Gell-Mann actually got his Nobel for the work he was doing at Caltech about the time I was there.Anyway, the two most famous professors in the department, and two of the most famous physicists in the world, had declared that my thesis was nonsense.That seminar was on a Friday.I spent the weekend formulating alternative career plans.I had always thought I would like to drive a Greyhound bus.That had always been my backup plan if I flunked out of college, so I was looking in the newspaper for open bus driver positions.I did not find any.On Monday I got up the courage to go talk to Bahcall.I expected to find him demolished, pondering career options like I was, but he seemed completely unphased by the experience.He told me not to worry about it, that he would straighten things out.He later talked the situation over with Feynman, who actually wound up spending a few days on the problem.In the end, he admitted we were right and he was wrong.To understand Gell-Mann's remarks, you had to understand department politics, of which I was totally unaware at that time.It turned out that Gell-Mann had an idea about how low-energy nuclear physics should be reformulated in a group-theoretic way, using the approach that had been very successful in particle physics.When he said that we should be thinking more, what he meant was that we should be doing the reaction-rate calculation by his new approach, which was a complete break from the conventional method for calculating weak interactions in nuclear physics.In our work in astrophysics, Bahcall and I had used a well-established method.Gell-Mann thought at that time that application of his approach would lead to tremendous new insights into the structure of nuclei.However, within a year or so, it became clear that the approach he had in mind for low-energy nuclear physics was not practical.
The lesson from this story is that even famous professors can be wrong.That does not mean that you should routinely ignore professors' advice.They are often right.But always bear in mind that they might be wrong.
More generally, do not worry too much if people do not accept your results right away.Be very careful in your work, and make sure you are right before you make a public presentation, but do not expect everybody to agree with your results right away.That is not how science works.

Do Not Be Afraid to Be Different
This is a point that Feynman stressed in his philosophizing.If you are a theorist, and if you want to find an explanation for something that has stumped other people, your best chance of success is to find a unique viewpoint.If you attack a problem using the same methods other people have used, and they didn't solve it, then you probably will not solve it either.The novelty of Feynman's approach was that he formulated most problems in terms of path integrals and variational principles.That allowed him to develop quantum electrodynamics, which was his greatest triumph and what earned him a Nobel Prize.After he did it his way, other people were able to translate it back into more conventionally rigorous theoretical framework.But his unique approach allowed Feynman to see it first.He used it with success in low-temperature physics and particle physics as well.Path integrals were Feynman's unique viewpoint.
I took Feynman's advice in my own career, and it has served me well.I started work on the Rice Convection Model (RCM) early in my career in space physics.(I will talk later about how that happened.)However, that gave me a viewpoint.For more than 50 years, I have viewed the magnetosphere from a Rice-Convection-Model point of view.It has given me a unique view of the world and has let me see several significant things first, even in situations that did not directly involve the RCM itself.
With regard to doing your own thing as a graduate student, you have to be a little reasonable.Remember that your professor is probably paying your lavish stipend from a grant that has specific objectives.It is uncomfortable and actually unethical for a professor to support a student doing his or her own thing, if that thing lies outside the scope of the grant.It is not a big problem for graduate students who are independently wealthy and do not need to be paid, but for everybody else it is a limitation.But within that constraint, if you can develop your own approach to things, that may prove to be a really big advantage for you.It is good to develop a unique viewpoint.

Do Not Hide Your Problems
My advisor John Bahcall went on to be a very influential astrophysicist.He did many things in astrophysics, but the thing he was most famous for was his work on solar neutrinos, which started in the early 60s and lasted through the rest of his career.
The reactions that power the Sun involve basically convert protons into He 4 .Since He 4 basically consists of 2 protons and 2 neutrons, that means that some of the source protons have to essentially change into neutrons, which requires beta decay.Beta decay is a weak interaction, which is part of the reason why it is taking the Sun billions of years to burn its hydrogen.There are different reaction chains involved, but they all involve beta decay and emission of a neutrino.The theory for all of this was pretty well refined by the late 1950s (Burbidge et al., 1957).People had made computer models of the Sun and were able to pretty much calculate the luminosity of the Sun pretty accurately from its composition and mass.The basic nuclear reaction rates could mostly be measured in the lab, and the results could be extrapolated to solar conditions by pretty solid theory.By the early 1960s, people were pretty sure what nuclear reactions were important in the Sun and they were pretty sure about their rates, despite the fact that they could not probe the center of the Sun.Somebody got the idea that they could test the well-developed theory of the solar interior if it were possible to measure neutrinos from the Sun.Neutrinos have such small cross sections for interactions with ordinary matter that they can go right from the center of the Sun to us.The downside of doing astronomy with particles that interact so weakly with matter is that you have to have a very large detector.Back in the 1960s people concluded that the easiest solar neutrinos to detect were those produced by the following reaction: which is one of the ones that theory says is happening in the solar interior.The neutrino comes off with about an MeV of energy, which is just enough to be detected by the reaction + 37  →  − + 37  An experimentalist named Ray Davis was in charge of a project aimed at measuring that reaction.It involved building a huge tank at the bottom of a gold mine in South Dakota.They filled the tank with hundreds of thousands of gallons of dry cleaning fluid, which contains lots of chlorine, and they looked for the argon.They would let the tank sit for months, and then bubble helium gas through the tank to sweep out the argon.Theory said that they would see a few argon atoms per month that way.It was really an incredibly sensitive experiment.Anyway, I remember Davis visiting Caltech in the mid-sixties.At that point, the work on the experiment was well underway but it was not clear whether it would work-that is, actually detect neutrinos.John Bahcall was the chief theorist who calculated the neutrino emission rates from theory, so he and Ray Davis were principally responsible for the quite expensive experiment.Of course, this experiment was a big gamble: they knew that they would be very embarrassed if the experiment found no neutrinos.At that time, I remember Bahcall saying that they had a plan for what to do if no neutrinos were found: they would open a dry-cleaning shop.Anyhow, they did see neutrinos (Davis et al., 1968).However, they saw about 1/3 as many as were predicted by the theoretical models.Of course, the experiment was repeated and improved.Bahcall and his collaborators went back to the models and tried varying uncertain parameters.Nuclear cross sections were measured more accurately.But all of that work did not bring the theoretical number down to what was observed.This went on for 20 years, in which they carefully studied every parameter that went into the models and did model runs covering the full reasonable range.The experimenters meanwhile kept refining the measurements.The discrepancy would not go away.The final explanation for the discrepancy was that the then-existing conventional theory for weak interactions was wrong.In that theory, neutrinos had zero mass.Neutrinos were thought to be completely stable, because a particle with no rest mass cannot decay into anything.The resolution of the solar neutrino problem was the discovery that neutrinos have nonzero mass.A neutrino wave function is a mixture of different kinds of neutrinos (electron, muon, and tau neutrinos).The particle oscillates between these different neutrino states.Only the electron neutrino can interact with chlorine.Only about 35% of the solar neutrinos are electron neutrinos.The rest are muon and tau neutrinos that had been formed from decay of the original electron neutrinos emitted by the Sun.That was the resolution of the solar neutrino problem (Bellerive, 2003).This was a remarkable case where theoretical astrophysics led to a discovery in particle physics.
The reason I went through this whole story is that this profound resolution of the solar neutrino problem happened because John Bahcall and his collaborators did not fudge their models to fit the observations.They carefully considered all of the variables and found that there was a real discrepancy.Finally, it turned out that the resolution of the problem was a profound step forward for particle physics.The message is: Do not fudge your results.If the theory does not agree with the data, and you cannot find a way to resolve the discrepancy, then publish the discrepancy, and try to honestly figure out why it exists.
Let me give you a more modest example from my own career.Back in the late 1970s, my group was starting to do event simulations with the RCM (Harel et al., 1981), and we were trying to develop an observation-based way of setting realistic boundary conditions.A key parameter was the value of the entropy function PV 5/3 at the tailward boundary, where P is pressure and V is the volume of the flux tube containing one unit of magnetic flux.There were no statistical models of the plasma sheet density, temperature, etc., at that time, but there were empirical magnetic field models.I assigned a new graduate student, Gary Erickson, to use those models to estimate PV 5/3 and, since we had flexibility as to where to put our boundary, I asked him to calculate PV 5/3 assuming various boundary locations.I expected that he would find that the answer would be approximately independent of the boundary location, because PV 5/3 is conserved in adiabatic drift.However, Gary found that the empirical-average value of PV 5/3 increased with distance.It varied by a factor of 3-5 for reasonable boundary locations.That meant that our model results were going to be sensitively dependent on where we put our boundary.It also meant that our model was in major disagreement with observations.Solid, simple theory said that PV 5/3 should be approximately conserved.Gary and I could not figure out how to resolve the problem, so we published the paper pointing out the discrepancy (Erickson & Wolf, 1980), which we called the pressure balance inconsistency.This was an odd theoretical paper.Normally, theoretical papers brag about how well their theory fits the data.In that 1980 paper, Gary and I demonstrated that our theory was wrong.
The attempt to resolve that discrepancy in the years since 1980 has led to the realization that plasma sheet transport is not a primarily more-or-less uniform sunward flow, which is what we had always imagined, but rather primarily in the form of bubbles of low-entropy plasma making their way to the inner plasma sheet (Angelopoulos et al., 1992;Chen & Wolf, 1993;Pontius & Wolf, 1990;Yang et al., 2014).
So the conclusion is: do not fudge your theory.Vary the parameters within the physically reasonable range.If the result still does not agree with the data, then admit the discrepancy and publish the paper.
Over the years, lots of people said we should paper over the pressure balance problem.There were suggestions that we should add artificial diffusion coefficients.I remember giving a talk about this once, when a senior experimentalist suggested that we should just change the adiabatic exponent, that is, assume PV n is conserved in adiabatic convection and adjust n to fit the statistical models.I replied that n = 5/3 was the theoretical value and that changing n would destroy the integrity of the theory.There was some giggling in the room at that point, and it was clear that some people did not find my argument convincing.However, that brief exchange raised a fundamental but controversial point.
To a lot of space plasma physicists, a good theory is one that agrees with the observations and a bad theory is one that does not.It does not matter whether the theory is logical or based on established physical laws.Agreement with the data is the only criterion.However, I fundamentally disagree with that.Suppose a theory is based on solid calculations solving basic laws of physics, and it does not agree with observations.That was the situation for both the solar neutrino problem and the pressure-balance inconsistency problem.If a sloppy theory with lots of approximations and little logic turns out to disagree with data, then it is pretty much useless.But if a theory that centers on careful solutions of well-grounded physical solid equations does not agree with observations, that theory is valuable.It points to a problem that cries out for really careful investigation.That is a situation where you have a chance to learn something important.

Find a Niche
Most academic scientists, to be successful in research, need to find a niche-some line of research that they can pursue better than anybody else.In practice, you really need to establish that kind of specialty to get sustained research funding.Feynman did not have to do that.He was so smart that he could jump from one field to another and make profound contributions.He did everything by himself, and his university paid his salary and provided him with paper and pencil.He did not need much more than that.However, for those of us who are not as smart as Feynman and need more support than paper and pencil, we have to write proposals and get grant support, and that, in practice, usually requires finding an area that you can call your own and in which you are an acknowledged expert.
Finding a niche is maybe the biggest challenge for young academic scientists at the postdoc stage of their careers.I do not have a general scheme for how to find it, but I will relate my experience.
When I finished my thesis at Caltech, I was very much aware that I had not found a niche.I was a postdoc for almost a year at Caltech and worked on a few other problems in theoretical astrophysics, but it was always a case of John Bahcall or somebody else pointing me at a problem.I was competent at solving problems once they were posed, but I had no idea how to find a good, solvable problem to work on.That was one of the reasons why I decided to switch to another field and took a job at Bell Labs.There I spent a year learning about space plasmas, which was a narrower area than astrophysics, but I still was not close to being able to find my own problem to work on.I was always working out problems that other people had suggested.I arrived at Rice in 1967 as an assistant professor.One day in 1968, Alex Dessler, the department chair, came into my office excited about an idea about how currents flow along field lines in the magnetosphere.He was drawing a picture of how protons and electrons would flow in the magnetosphere in the presence of a convection electric field, which was known to exist by that time.His picture sounded right but it consisted entirely of cartoons.A memorable paper by Schield et al. (1969), came out of that idea.It was a theoretical paper with no equations and no calculations.Just cartoons.Actually there were a couple of simple in-line equations, but nothing substantial enough to justify the expenditure of an equation number.Here was a problem that just cried out to be computer modeled.I figured that was maybe the niche I had been looking for.So I dropped what I was doing and started working on that computer model (Wolf, 1970), which became the RCM.In looking for a niche, it is important to find a niche that is big enough to contain a line of research, not just one paper.Of course, in 1968 I could see that the problem Alex suggested was big, but I did not know how big.I had no idea that I would still be working on that problem more than 50 years later.

Summary
I have attempted to convey five bits of insight gleaned in the course of 60 years of research, insights into how to do scientific research effectively.I was intimately involved in some of the research, but some of it I learned from seminars, lectures, and conversations.My arguments came from examples from astrophysics and space physics, but they are applicable to almost all areas of physics.
However, the reader should be warned that some of the examples came from stories were recalled from decades ago and resist rigorous fact checking.