In my latest post I talked about some of the reasons that may induce professional scientists to redirect their research effort to different fields of inquiry, after working on a given problem, or in a certain area, for an extended period of time. In my view, there are valid and not so valid reasons for taking such a course of action. In my latest post, I talked about the valid ones.
Today, I shall expound some arguments for making such a change which I have heard in the course of my career, which I have always found unconvincing, shallow, and ultimately flawed (the arguments, silly, not the career). They are mostly borne out of opportunism, misinformation as well as what someone in the past might have referred to as “fuzzy math”. Personally, I am glad I did not heed those calls. Switching field based on one of these arguments is not likely to do anything useful for one’s scientific fortunes, whether that be in academia or outside.
In my previous post I remained purposefully vague as to what constitutes “change”. It need not be a migration into a completely different discipline (e.g., from physics to economics), it could be also something that one may merely regard as an “excursion” into nearby territory (e.g., from high-temperature superconductivity to colossal magnetoresistance, for a condensed matter physicist). Here, we shall simply assume that change involve familiarizing with new literature, establishing new collaborations and scientific ties, attending different conferences, and possibly learning new tools.
As I mentioned in my previous post, intellectual curiosity, breadth, the emergence of new interests, the desire to explore something different, often in concomitance with a feeling of exhaustion and tiredness for a subject that has taken the best of our waking time for a number of years, the sense that one’s research program has run its course (possibly due to its successful conclusion), are all acceptable, understandable, “legitimate” motives for making a change.
So, on to the phoney ones:
This looks too difficult — it must be a stupid problem
Of course, no one will ever phrase it in those terms. “I am giving up on this problem, because it is just too damn difficult for me“, would amount to conceding defeat. The preferred language is, for example, that used in my presence by the chair of a respectable, mid-size physics department, at dinner time — it was at a recent APS meeting. In a long, inconsequential tirade, the man lamented the inability of many of us in condensed matter physics to “break free from obsolete dicta“, to “think outside the box”, our insistence to work on “old”, “boring” problems, which “never went anywhere” “without any relevance to society”, instead of embracing “new thinking”, focusing on “non-traditional”, “strategically relevant” questions.
OK, now, what might be, according to him, the “old”, “boring” problems, with no relevance to society ? Why, but the difficult, fundamental ones that are still unsolved, of course (that is what “never went anywhere” means) — high-temperature superconductivity being the chief example — the ones on which scores of talented (and not so talented) scientists have banged their heads without cracking them (the problems, that is, not the heads… him being one of them, of course). And what about the “strategically relevant” ones ? Well, you guessed it — nano-this, bio-that, and in general problems whose
fundamental actual physics content is slim to none (never mind the fact that we are inarguably talking even “older” physics), but which are “more down to earth” (read: easier) and with some (true or alleged) connection with (supposedly) “applied” areas of science .
As long as it is just one, or few isolated individuals talking such nonsense (disconcerting as it is that a physics department should pick someone with this “vision” for chair), the damage will be limited. Unfortunately, this irrational, defeatist kind of thinking can be at times pervasive, to the point of actually affecting those with decision making power, i.e., faculty search committee members, science deans, funding agencies and program directors .
Since when do scientists abandon a problem because it is too difficult (and blame the problem for that !) ? To me, telling a scientist to stop working on a problem because it’s too difficult, that “if she were meant to solve it she would have solved it by now”, and that she should focus on something easier instead, makes just about as much sense as telling an aspiring musician that the symphony she’s working on will never be a success, hence she might as well write music for TV commercials…
One can surely understand the frustration and disappointment over lack of success on the part of the community at unraveling a mystery whose key seemed so within reach only a decade back. At the same time, one ought not make the mistake of throwing the baby out with the bath water, and declare science “dead” (as some did), just because the easy problems have been solved and the ones that remain are hard.
I am not saying that one should insist with trying to solve the same problem from graduate school until retirement; yes, there may come a time when wrapping up what we have done and moving on to something different, something which stimulates us and captures our imagination just like the previous subject did, at some point in the past, may be the right thing to do. However, moving on to another subject just because it seems “easier”, is not the way to go. Scientists should never forget that they did not make this life choice, pick this career, so that some day they would solve “easy” problems. The excuse that someone else may find useful our solutions to their easy problems, seems like a futile consolation — let them find it.
Where is the money ?
Perhaps even more disturbing and pernicious, is the idea that the choice of research field or subject should be to a large extent driven by the chance of being funded. Especially for junior faculty tracking tenure, funding can become a real obsession, as many convince themselves that their worthiness of retention will be assessed by their institution largely based on the sheer amount of money that they will be able to bring in. In other words, from means to an end, funding becomes an end to itself — to the point where one would leave a particular field or discipline due to scarcity of funding, and pick a new research topic based on the projected success at attracting monies needed to sustain research. I think that this notion is dismal, and frankly nonsensical.
I distinctly remember thinking that there was something funny about what I was hearing, the very first time I was told by a reputable senior scientist, about sixteen years ago, that it would be crazy for me to continue to do research on my favourite subject for the simple reason that it was not “fundable”.
“This is how I decide if anything is worth doing, these days. I ask myself ‘is it fundable ?’. If the answer is ‘no’, I move on“.
There are obviously good reasons for going after funding. These days, any worthwhile research endeavour is expensive, and without guaranteed access to equipment and/or materials, as well as sufficient manpower, one’s research ambition may be all but doomed. That means that one’s research program should be realistically tailored to one’s likelihood to bring in the kind of funding needed to sustain it in time — all of this is common sense . But, from that to making funding likelihood the main criterion to pick the area, or subject on which one will be spending time researching for years, educating graduate and undergraduate students, talking to others and possibly teaching in the classroom, there seems to be quite a leap. I think interest and passion for what one is studying remain essential ingredients to a successful career in science, and the notion that one can develop passion for whatever subject is deemed worthwhile by private sector and politicians, seems dubious.
And, lest one forget: it is a fallacy to assume that, just because the pot of monies to distribute around is bigger, then one’s individual grant will also be (this would be the “fuzzy math” to which I was referring above). For, the overall budget reflects the number of investigators engaged in research in that area. So yes, there may be more money to be had, but the number of scientists against whom one is competing for a slice of the pie is also greater . I have personally never regretted sticking with my favourite subject. Funding has never been great, but has never vanished either. My observation is that scientists who come to be regarded as leading investigators in relatively small, not necessarily “hot” fields, often have a pretty good life.
Piece of cake
“Do you realize that, with your background in quantum simulations, it would be a piece of cake for you to work on polymers ? I mean, seriously, people working in that area have no clue… You could start today and be their messiah tomorrow…” (same person who said that my research subject was nor fundable, circa 1995).
Haven’t we all heard nonsense like that ? What exactly makes people think that they can walk into another turf like an explorer from the old world venturing into a primitive land, expecting to instil its native inhabitants with a sense of awe, at the sight of fire magically produced from nowhere, with the sole aid of a magnifying glass ? Am I the only one to find such a conceited attitude utterly ridiculous ?
The tendency for someone who, in the course of many years of hard work, has acquired in-depth knowledge of a field of inquiry and its tools and methodologies, to believe that said knowledge ought be relevant in other areas as well, is perhaps understandable. We all wish our hard work to be “recyclable”, to a degree, and I think no scientist is immune from that . However, one should think twice before making a move into a different discipline (or a brand new field, conceptually distant from that with which one is familiar), if the expectation of having a technical edge over its “natural” occupants is the main reason for doing it.
First off, even though I am not dismissing it as a possible scenario, I think it happens seldom. The fact that we have come up with one good mouse trap does not mean that that is the only, or the best mouse trap. And, people in other disciplines are not stupid. They may not be familiar with tools that are not traditionally part of their academic background, but that does not mean that they cannot pick them up quickly. Any initial advantage is going to be short-lived.
Secondly, if one is thinking of establishing in the long run an independent, successful program as principal investigator, the toll to pay to the lack of basic knowledge of that field (the one that one acquires by pursuing a doctoral degree) may be significant. There is an issue of credibility in the eyes of program directors, as well as of potential students, postdocs and collaborators. You may indeed have formidable tools in your hands, but do you know what to use them for ? Are you going to spend months and months going through the literature, just to catch up and figure out what is worth doing (or even if there is something worth doing for you)  ? Or, are you going to collaborate with a senior scientist in that discipline, one with an established reputation, who can tell you what to “aim your cannon” at ? In this case, you may be destined to play permanently the role of “support technician”, the scientific leadership remaining firmly in the hands of the person who was in that field before you. Is that something you are willing to accept ?
I know I am not.
 All of this was very nebulously phrased, not surprisingly given that the person himself is a (former) condensed matter theorist, who, by his own admission, failed to make any contribution, something that he squarely blames on the fields and problems on which he worked. I could not ascertain whether he had any real knowledge of the murky “practical applications” he was talking about. But, don’t get me wrong, I have nothing against nano or bio (some of my best friends…). I am not one of those who will dismiss anything “nano” by saying that 90% of it is just hype, or fancily worded, disingenuous repackaging of old stuff — not until I see the remaining 10% anyway. Kidding. Not really. Yes, I am. Maybe.
 I have witnessed this kind of Orwellian turnabout a few times in my (not so long) career. Topics of research which until the day before were regarded as compelling, fascinating, challenging, of milestone importance, attracting and engaging the brightest minds, suddenly turn into exercises in vacuity, wastes of precious resources, tiresome rehashing of “old science”, quackery. Junior scientists insisting with their hopeless, ostensibly doomed pursuits of answers to those still unsolved riddles (now so démodé), are labeled as naive and delusional. After all, how could these people possibly succeed where their older colleagues failed ? Someone should really talk some sense in the head of these modern Don Quixotes, convince them to abandon their grandiose ambitions and work instead on something boring but easier…
For a much more serious, authoritative and eloquent statement, you may read this editorial.
 But there are things that one can do, strategies that one can adopt that can limit one’s dependence on extramural funding. I think that there is something wrong if a tenure-track assistant professor finds herself spending more than a few hours a month writing grant proposals.
 I would be curious to know, for example, how many condensed matter physicists who migrated toward biophysics (a popular trend in the late 90s) saw a substantial increase in their annual extramural funding.
 We physicists take that notion to a whole new level. And it is not because we are an arrogant bunch — not at all. It is a simple fact that we just know better. Look, we all know that physicists routinely make dramatic advances in other fields possible, owing to superior thinking abilities, experimental skills, and the sophisticated analytical and numerical tools that we invent… says who, you ask ? Why, but physicists, of course ! What, are you going to tell me that biologists, geologists, economists, engineers, physicians, chemists etc. would take issue with that contention ? That they would say that most, if not all that physicists have had to contribute to their fields, was irrelevant bs ? Ah, what do they know, anyway … show me one of them who has ever solved a single problem from Jackson’s book … Are you going to tell me that there is a reason why breakthroughs on these subjects made by physicists end up published on a physics journal, rather than on flagship publications specific to those areas ? Because, if that is what you are thinking, then you must not be a physicist…
 Case in point: yes, I probably can use my quantum many-body Monte Carlo codes to simulate polymers. Question: what the heck am I supposed to calculate ? What are the outstanding scientific issues ? If I have to find out on my own it is going to take me a long time. And, why is my computational methodology any better than that which people in the field of polymers are already using ?