Tag Archives: DoingScience

What You’re Actually Scared of in Impostor Syndrome

Academics tend to face a lot of impostor syndrome. Something about a job with no clear criteria for success, where you could always in principle do better and you mostly only see the cleaned-up, idealized version of others’ work, is a recipe for driving people utterly insane with fear.

The way most of us talk about that fear, it can seem like a cognitive bias, like a failure of epistemology. “Competent people think they’re less competent than they are,” the less-discussed half of the Dunning-Kruger effect.

(I’ve talked about it that way before. And, in an impostor-syndrome-inducing turn of events, I got quoted in a news piece in Nature about it.)

There’s something missing in that perspective, though. It doesn’t really get across how impostor syndrome feels. There’s something very raw about it, something that feels much more personal and urgent than an ordinary biased self-assessment.

To get at the core of it, let me ask a question: what happens to impostors?

The simple answer, the part everyone will admit to, is to say they stop getting grants, or stop getting jobs. Someone figures out they can’t do what they claim, and stops choosing them to receive limited resources. Pretty much anyone with impostor syndrome will say that they fear this: the moment that they reach too far, and the world decides they aren’t worth the money after all.

In practice, it’s not even clear that that happens. You might have people in your field who are actually thought of as impostors, on some level. People who get snarked about behind their back, people where everyone rolls their eyes when they ask a question at a conference and the question just never ends. People who are thought of as shiny storytellers without substance, who spin a tale for journalists but aren’t accomplishing anything of note. Those people…aren’t facing consequences at all, really! They keep getting the grants, they keep finding the jobs, and the ranks of people leaving for industry are instead mostly filled with those you respect.

Instead, I think what we fear when we feel impostor syndrome isn’t the obvious consequence, or even the real consequence, but something more primal. Primatologists and psychologists talk about our social brain, and the role of ostracism. They talk about baboons who piss off the alpha and get beat up and cast out of the group, how a social animal on their own risks starvation and becomes easy prey for bigger predators.

I think when we wake up in a cold sweat remembering how we had no idea what that talk was about, and were too afraid to ask, it’s a fear on that level that’s echoing around in our heads. That the grinding jags of adrenaline, the run-away-and-hide feeling of never being good enough, the desperate unsteadiness of trying to sound competent when you’re sure that you’re not and will get discovered at any moment…that’s not based on any realistic fears about what would happen if you got caught. That’s your monkey-brain, telling you a story drilled down deep by evolution.

Does that help? I’m not sure. If you manage to tell your inner monkey that it won’t get eaten by a lion if its friends stop liking it, let me know!

I Have a Theory

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“I have a theory,” says the scientist in the book. But what does that mean? What does it mean to “have” a theory?

First, there’s the everyday sense. When you say “I have a theory”, you’re talking about an educated guess. You think you know why something happened, and you want to check your idea and get feedback. A pedant would tell you you don’t really have a theory, you have a hypothesis. It’s “your” hypothesis, “your theory”, because it’s what you think happened.

The pedant would insist that “theory” means something else. A theory isn’t a guess, even an educated guess. It’s an explanation with evidence, tested and refined in many different contexts in many different ways, a whole framework for understanding the world, the most solid knowledge science can provide. Despite the pedant’s insistence, that isn’t the only way scientists use the word “theory”. But it is a common one, and a central one. You don’t really “have” a theory like this, though, except in the sense that we all do. These are explanations with broad consensus, things you either know of or don’t, they don’t belong to one person or another.

Except, that is, if one person takes credit for them. We sometimes say “Darwin’s theory of evolution”, or “Einstein’s theory of relativity”. In that sense, we could say that Einstein had a theory, or that Darwin had a theory.

Sometimes, though, “theory” doesn’t mean this standard official definition, even when scientists say it. And that changes what it means to “have” a theory.

For some researchers, a theory is a lens with which to view the world. This happens sometimes in physics, where you’ll find experts who want to think about a situation in terms of thermodynamics, or in terms of a technique called Effective Field Theory. It happens in mathematics, where some choose to analyze an idea with category theory not to prove new things about it, but just to translate it into category theory lingo. It’s most common, though, in the humanities, where researchers often specialize in a particular “interpretive framework”.

For some, a theory is a hypothesis, but also a pet project. There are physicists who come up with an idea (maybe there’s a variant of gravity with mass! maybe dark energy is changing!) and then focus their work around that idea. That includes coming up with ways to test whether the idea is true, showing the idea is consistent, and understanding what variants of the idea could be proposed. These ideas are hypotheses, in that they’re something the scientist thinks could be true. But they’re also ideas with many moving parts that motivate work by themselves.

Taken to the extreme, this kind of “having” a theory can go from healthy science to political bickering. Instead of viewing an idea as a hypothesis you might or might not confirm, it can become a platform to fight for. Instead of investigating consistency and proposing tests, you focus on arguing against objections and disproving your rivals. This sometimes happens in science, especially in more embattled areas, but it happens much more often with crackpots, where people who have never really seen science done can decide it’s time for their idea, right or wrong.

Finally, sometimes someone “has” a theory that isn’t a hypothesis at all. In theoretical physics, a “theory” can refer to a complete framework, even if that framework isn’t actually supposed to describe the real world. Some people spend time focusing on a particular framework of this kind, understanding its properties in the hope of getting broader insights. By becoming an expert on one particular theory, they can be said to “have” that theory.

Bonus question: in what sense do string theorists “have” string theory?

You might imagine that string theory is an interpretive framework, like category theory, with string theorists coming up with the “string version” of things others understand in other ways. This, for the most part, doesn’t happen. Without knowing whether string theory is true, there isn’t much benefit in just translating other things to string theory terms, and people for the most part know this.

For some, string theory is a pet project hypothesis. There is a community of people who try to get predictions out of string theory, or who investigate whether string theory is consistent. It’s not a huge number of people, but it exists. A few of these people can get more combative, or make unwarranted assumptions based on dedication to string theory in particular: for example, you’ll see the occasional argument that because something is difficult in string theory it must be impossible in any theory of quantum gravity. You see a spectrum in the community, from people for whom string theory is a promising project to people for whom it is a position that needs to be defended and argued for.

For the rest, the question of whether string theory describes the real world takes a back seat. They’re people who “have” string theory in the sense that they’re experts, and they use the theory primarily as a mathematical laboratory to learn broader things about how physics works. If you ask them, they might still say that they hypothesize string theory is true. But for most of these people, that question isn’t central to their work.

Integration by Parts, Evolved

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I posted what may be my last academic paper today, about a project I’ve been working on with Matthias Wilhelm for most of the last year. The paper is now online here. For me, the project has been a chance to broaden my horizons, learn new skills, and start to step out of my academic comfort zone. For Matthias, I hope it was grant money well spent.

I wanted to work on something related to machine learning, for the usual trendy employability reasons. Matthias was already working with machine learning, but was interested in pursuing a different question.

When is machine learning worthwhile? Machine learning methods are heuristics, unreliable methods that sometimes work well. You don’t use a heuristic if you have a reliable method that runs fast enough. But if all you have are heuristics to begin with, then machine learning can give you a better heuristic.

Matthias noticed a heuristic embedded deep in how we do particle physics, and guessed that we could do better. In particle physics, we use pictures called Feynman diagrams to predict the probabilities for different outcomes of collisions, comparing those predictions to observation to look for evidence of new physics. Each Feynman diagram corresponds to an integral, and for each calculation there are hundreds, thousands, or even millions of those integrals to do.

Luckily, physicists don’t actually have to do all those integrals. It turns out that most of them are related, by a slightly more advanced version of that calculus class mainstay, integration by parts. Using integration by parts you can solve a list of equations, finding out how to write your integrals in terms of a much smaller list.

How big a list of equations do you need, and which ones? Twenty-five years ago, Stefano Laporta proposed a “golden rule” to choose, based on his own experience, and people have been using it (more or less, with their own tweaks) since then.

Laporta’s rule is a heuristic, with no proof that it is the best option, or even that it will always work. So we probably shouldn’t have been surprised when someone came up with a better heuristic. Watching talks at a December 2023 conference, Matthias saw a presentation by Johann Usovitsch on a curious new rule. The rule was surprisingly simple, just one extra condition on top of Laporta’s. But it was enough to reduce the number of equations by a factor of twenty.

That’s great progress, but it’s also a bit frustrating. Over almost twenty-five years, no-one had guessed this one simple change?

Maybe, thought Matthias and I, we need to get better at guessing.

We started out thinking we’d try reinforcement learning, a technique where a machine is trained by playing a game again and again, changing its strategy when that strategy brings it a reward. We thought we could have the machine learn to cut away extra equations, getting rewarded if it could cut more while still getting the right answer. We didn’t end up pursuing this very far before realizing another strategy would be a better fit.

What is a rule, but a program? Laporta’s golden rule and Johann’s new rule could both be expressed as simple programs. So we decided to use a method that could guess programs.

One method stood out for sheer trendiness and audacity: FunSearch. FunSearch is a type of algorithm called a genetic algorithm, which tries to mimic evolution. It makes a population of different programs, “breeds” them with each other to create new programs, and periodically selects out the ones that perform best. That’s not the trendy or audacious part, though, people have been doing that sort of genetic programming for a long time.

The trendy, audacious part is that FunSearch generates these programs with a Large Language Model, or LLM (the type of technology behind ChatGPT). Using an LLM trained to complete code, FunSearch presents the model with two programs labeled v0 and v1 and asks it to complete v2. In general, program v2 will have some traits from v0 and v1, but also a lot of variation due to the unpredictable output of LLMs. The inventors of FunSearch used this to contribute the variation needed for evolution, using it to evolve programs to find better solutions to math problems.

We decided to try FunSearch on our problem, modifying it a bit to fit the case. We asked it to find a shorter list of equations, giving a better score for a shorter list but a penalty if the list wasn’t able to solve the problem fully.

Some tinkering and headaches later, it worked! After a few days and thousands of program guesses, FunSearch was able to find a program that reproduced the new rule Johann had presented. A few hours more, and it even found a rule that was slightly better!

But then we started wondering: do we actually need days of GPU time to do this?

An expert on heuristics we knew had insisted, at the beginning, that we try something simpler. The approach we tried then didn’t work. But after running into some people using genetic programming at a conference last year, we decided to try again, using a Python package they used in their work. This time, it worked like a charm, taking hours rather than days to find good rules.

This was all pretty cool, a great opportunity for me to cut my teeth on Python programming and its various attendant skills. And it’s been inspiring, with Matthias drawing together more people interested in seeing just how much these kinds of heuristic methods can do there. I should be clear though, that so far I don’t think our result is useful. We did better than the state of the art on an example, but only slightly, and in a way that I’d guess doesn’t generalize. And we needed quite a bit of overhead to do it. Ultimately, while I suspect there’s something useful to find in this direction, it’s going to require more collaboration, both with people using the existing methods who know better what the bottlenecks are, and with experts in these, and other, kinds of heuristics.

So I’m curious to see what the future holds. And for the moment, happy that I got to try this out!

Physics Gets Easier, Then Harder

Lack of Recognition Is a Symptom, Not a Cause

The Bystander Effect for Reviewers

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I probably came off last week as a bit of an extreme “journal abolitionist”. This week, I wanted to give a couple caveats.

First, as a commenter pointed out, the main journals we use in my field are run by nonprofits. Physical Review Letters, the journal where we publish five-page papers about flashy results, is run by the American Physical Society. The Journal of High-Energy Physics, where we publish almost everything else, is run by SISSA, the International School for Advanced Studies in Trieste. (SISSA does use Springer, a regular for-profit publisher, to do the actual publishing.)

The journals are also funded collectively, something I pointed out here before but might not have been obvious to readers of last week’s post. There is an agreement, SCOAP3, where research institutions band together to pay the journals. Authors don’t have to pay to publish, and individual libraries don’t have to pay for subscriptions.

And this is a lot better than the situation in other fields, yeah! Though I’d love to quantify how much. I haven’t been able to find a detailed breakdown, but SCOAP3 pays around 1200 EUR per article published. What I’d like to do (but not this week) is to compare this to what other fields pay, as well as to publishing that doesn’t have the same sort of trapped audience, and to online-only free journals like SciPost. (For example, publishing actual physical copies of journals at this point is sort of a vanity thing, so maybe we should compare costs to vanity publishers?)

Second, there’s reviewing itself. Even without traditional journals, one might still want to keep peer review.

What I wanted to understand last week was what peer review does right now, in my field. We read papers fresh off the arXiv, before they’ve gone through peer review. Authors aren’t forced to update the arXiv with the journal version of their paper, if they want another version, even if that version was rejected by the reviewers, then they’re free to do so, and most of us wouldn’t notice. And the sort of in-depth review that happens in peer review also happens without it. When we have journal clubs and nominate someone to present a recent paper, or when we try to build on a result or figure out why it contradicts something we thought we knew, we go through the same kind of in-depth reading that (in the best cases) reviewers do.

But I think I’ve hit upon something review does that those kinds of informal things don’t. It gets us to speak up about it.

I presented at a journal club recently. I read through a bombastic new paper, figured out what I thought was wrong with it, and explained it to my colleagues.

But did I reach out to the author? No, of course not, that would be weird.

Psychologists talk about the bystander effect. If someone collapses on the street, and you’re the only person nearby, you’ll help. If you’re one of many, you’ll wait and see if someone else helps instead.

I think there’s a bystander effect for correcting people. If someone makes a mistake and publishes something wrong, we’ll gripe about it to each other. But typically, we won’t feel like it’s our place to tell the author. We might get into a frustrating argument, there wouldn’t be much in it for us, and it might hurt our reputation if the author is well-liked.

(People do speak up when they have something to gain, of course. That’s why when you write a paper, most of the people emailing you won’t be criticizing the science: they’ll be telling you you need to cite them.)

Peer review changes the expectations. Suddenly, you’re expected to criticize, it’s your social role. And you’re typically anonymous, you don’t have to worry about the consequences. It becomes a lot easier to say what you really think.

(It also becomes quite easy to say lazy stupid things, of course. This is why I like setups like SciPost, where reviews are made public even when the reviewers are anonymous. It encourages people to put some effort in, and it means that others can see that a paper was rejected for bad reasons and put less stock in the rejection.)

I think any new structure we put in place should keep this feature. We need to preserve some way to designate someone a critic, to give someone a social role that lets them let loose and explain why someone else is wrong. And having these designated critics around does help my field. The good criticisms get implemented in the papers, the authors put the new versions up on arXiv. Reviewing papers for journals does make our science better…even if none of us read the journal itself.

HAMLET-Physics 2024

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Back in January, I announced I was leaving France and leaving academia. Since then, it hasn’t made much sense for me to go to conferences, even the big conference of my sub-field or the conference I organized.

I did go to a conference this week, though. I had two excuses:

The conference was here in Copenhagen, so no travel required.
The conference was about machine learning.

HAMLET-Physics, or How to Apply Machine Learning to Experimental and Theoretical Physics, had the additional advantage of having an amusing acronym. Thanks to generous support by Carlsberg and the Danish Data Science Academy, they could back up their choice by taking everyone on a tour of Kronborg (better known in the English-speaking world as Elsinore).

This conference’s purpose was to bring together physicists who use machine learning, machine learning-ists who might have something useful to say to those physicists, and other physicists who don’t use machine learning yet but have a sneaking suspicion they might have to at some point. As a result, the conference was super-interdisciplinary, with talks by people addressing very different problems with very different methods.

Interdisciplinary conferences are tricky. It’s easy for the different groups of people to just talk past each other: everyone shows up, gives the same talk they always do, socializes with the same friends they always meet, then leaves.

There were a few talks that hit that mold, and were so technical only a few people understood. But most were better. The majority of the speakers did really well at presenting their work in a way that would be understandable and even exciting to people outside their field, while still having enough detail that we all learned something. I was particularly impressed by Thea Aarestad’s keynote talk on Tuesday, a really engaging view of how machine learning can be used under the extremely tight time constraints LHC experiments need to decide whether to record incoming data.

For the social aspect, the organizers had a cute/gimmicky/machine-learning-themed solution. Based on short descriptions and our public research profiles, they clustered attendees, plotting the connections between them. They then used ChatGPT to write conversation prompts between any two people on the basis of their shared interests. In practice, this turned out to be amusing but totally unnecessary. We were drawn to speak to each other not by conversation prompts, but by a drive to learn from each other. “Why do you do it that way?” was a powerful conversation-starter, as was “what’s the best way to do this?” Despite the different fields, the shared methodologies gave us strong reasons to talk, and meant that people were very rarely motivated to pick one of ChatGPT’s “suggestions”.

Overall, I got a better feeling for how machine learning is useful in physics (and am planning a post on that in future). I also got some fresh ideas for what to do myself, and a bit of a picture of what the future holds in store.

Toy Models

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In academia, scientists don’t always work with what they actually care about. A lot of the time, they use what academics call toy models. A toy model can be a theory with simpler mathematics than the theories that describe the real world, but it can also be something that is itself real, just simpler or easier to work with, like nematodes, fruit flies, or college students.

Some people in industry seem to think this is all academics do. I’ve seen a few job ads that emphasize experience dealing with “real-world data”, and a few people skeptical that someone used to academia would be able to deal with the messy challenges of the business world.

There’s a grain of truth to this, but I don’t think industry has a monopoly on mess. To see why, let’s think about how academics write computer code.

There are a lot of things that one is in-principle supposed to do to code well, and most academics do none of them. Good code has test suites, so that if you change something you can check whether it still works by testing it on all the things that could go wrong. Good code is modular, with functions doing specific things and re-used whenever appropriate. Good code follows shared conventions, so that others can pick up your code and understand how you did it.

Some academics do these things, for example those who build numerical simulations on supercomputers. But for most academics, coding best-practices range from impractical to outright counterproductive. Testing is perhaps the clearest example. To design a test suite, you have to have some idea what kinds of things your code will run into, what kind of input you expect what the output is supposed to be. Many academic projects, though, are the first of their kind. Academics code up something to do a calculation nobody has done before, not knowing the result, or they make code to analyze a dataset nobody has worked with before. By the time they understand the problem well enough to write a test suite, they’ve already solved the problem, and they’re on to the next project, which may need something totally different.

From the perspective of these academics, if you have a problem well-defined enough that you can build a test suite, well enough that you can have stable conventions and reusable functions…then you have a toy model, not a real problem from the real world.

…and of course, that’s not quite fair either, right?

The truth is, academics and businesspeople want to work with toy models. Toy models are well-behaved, and easy, and you can do a lot with them. The real world isn’t a toy model…but it can be, if you make it one.

This means planning your experiments, whether in business or in science. It means making sure the data you gather is labeled and organized before you begin. It means coming up with processes, and procedures, and making as much of the work as possible a standardized, replicable thing. That’s desirable regardless, whether you’re making a consistent product instead of artisanal one-offs or a well-documented scientific study that another team can replicate.

Academia and industry both must handle mess. They handle different kinds of mess in different circumstances, and manage it in different ways, and this can be a real challenge for someone trying to go from one world to another. But neither world is intrinsically messier or cleaner. Nobody has a monopoly on toy models.

Does Science Require Publication?

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Seen on Twitter:

As is traditional, twitter erupted into dumb arguments over this. Some made fun of Yann LeCun for implying that Elon Musk will be forgotten, which despite any other faults of his seems unlikely. Science popularizer Sabine Hossenfelder pointed out that there are two senses of “publish” getting confused here: publish as in “make public” and publish as in “put in a scientific journal”. The latter tends to be necessary for scientists in practice, but is not required in principle. (The way journals work has changed a lot over just the last century!) The former, Sabine argued, is still 100% necessary.

Plenty of people on twitter still disagreed (this always happens). It got me thinking a bit about the role of publication in science.

When we talk about what science requires or doesn’t require, what are we actually talking about?

“Science” is a word, and like any word its meaning is determined by how it is used. Scientists use the word “science” of course, as do schools and governments and journalists. But if we’re getting into arguments about what does or does not count as science, then we’re asking about a philosophical problem, one in which philosophers of science try to understand what counts as science and what doesn’t.

What do philosophers of science want? Many things, but a big one is to explain why science works so well. Over a few centuries, humanity went from understanding the world in terms of familiar materials and living creatures to decomposing them in terms of molecules and atoms and cells and proteins. In doing this, we radically changed what we were capable of, computers out of the reach of blacksmiths and cures for diseases that weren’t even distinguishable. And while other human endeavors have seen some progress over this time (democracy, human rights…), science’s accomplishment demands an explanation.

Part of that explanation, I think, has to include making results public. Alchemists were interested in many of the things later chemists were, and had started to get some valuable insights. But alchemists were fearful of what their knowledge would bring (especially the ones who actually thought they could turn lead into gold). They published almost only in code. As such, the pieces of progress they made didn’t build up, didn’t aggregate, didn’t become overall progress. It was only when a new scientific culture emerged, when natural philosophers and physicists and chemists started writing to each other as clearly as they could, that knowledge began to build on itself.

Some on twitter pointed out the example of the Manhattan project during World War II. A group of scientists got together and made progress on something almost entirely in secret. Does that not count as science?

I’m willing to bite this bullet: I don’t think it does! When the Soviets tried to replicate the bomb, they mostly had to start from scratch, aside from some smuggled atomic secrets. Today, nations trying to build their own bombs know more, but they still must reinvent most of it. We may think this is a good thing, we may not want more countries to make progress in this way. But I don’t think we can deny that it genuinely does slow progress!

At the same time, to contradict myself a bit: I think you can think of science that happens within a particular community. The scientists of the Manhattan project didn’t publish in journals the Soviets could read. But they did write internal reports, they did publish to each other. I don’t think science by its nature has to include the whole of humanity (if it does, then perhaps studying the inside of black holes really is unscientific). You probably can do science sticking to just your own little world. But it will be slower. Better, for progress’s sake, if you can include people from across the world.

No Unmoved Movers

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Economists must find academics confusing.

When investors put money in a company, they have some control over what that company does. They vote to decide a board, and the board votes to hire a CEO. If the company isn’t doing what the investors want, the board can fire the CEO, or the investors can vote in a new board. Everybody is incentivized to do what the people who gave the money want to happen. And usually, those people want the company to increase its profits, since most of them people are companies with their own investors).

Academics are paid by universities and research centers, funded in the aggregate by governments and student tuition and endowments from donors. But individually, they’re also often funded by grants.

What grant-givers want is more ambiguous. The money comes in big lumps from governments and private foundations, which generally want something vague like “scientific progress”. The actual decision of who gets the money are made by committees made up of senior scientists. These people aren’t experts in every topic, so they have to extrapolate, much as investors have to guess whether a new company will be profitable based on past experience. At their best, they use their deep familiarity with scientific research to judge which projects are most likely to work, and which have the most interesting payoffs. At their weakest, though, they stick with ideas they’ve heard of, things they know work because they’ve seen them work before. That, in a nutshell, is why mainstream research prevails: not because the mainstream wants to suppress alternatives, but because sometimes the only way to guess if something will work is raw familiarity.

(What “works” means is another question. The cynical answers are “publishes papers” or “gets citations”, but that’s a bit unfair: in Europe and the US, most funders know that these numbers don’t tell the whole story. The trivial answer is “achieves what you said it would”, but that can’t be the whole story, because some goals are more pointless than others. You might want the answer to be “benefits humanity”, but that’s almost impossible to judge. So in the end the answer is “sounds like good science”, which is vulnerable to all the fads you can imagine…but is pretty much our only option, regardless.)

So are academics incentivized to do what the grant committees want? Sort of.

Science never goes according to plan. Grant committees are made up of scientists, so they know that. So while many grants have a review process afterwards to see whether you achieved what you planned, they aren’t all that picky about it. If you can tell a good story, you can explain why you moved away from your original proposal. You can say the original idea inspired a new direction, or that it became clear that a new approach was necessary. I’ve done this with an EU grant, and they were fine with it.

Looking at this, you might imagine that an academic who’s a half-capable storyteller could get away with anything they wanted. Propose a fashionable project, work on what you actually care about, and tell a good story afterwards to avoid getting in trouble. As long as you’re not literally embezzling the money (the guy who was paying himself rent out of his visitor funding, for instance), what could go wrong? You get the money without the incentives, you move the scientific world and nobody gets to move you.

It’s not quite that easy, though.

Sabine Hossenfelder told herself she could do something like this. She got grants for fashionable topics she thought were pointless, and told herself she’d spend time on the side on the things she felt were actually important. Eventually, she realized she wasn’t actually doing the important things: the faddish research ended up taking all her time. Not able to get grants doing what she actually cared about (and, in one of those weird temporary European positions that only lasts until you run out of grants), she now has to make a living from her science popularization work.

I can’t speak for Hossenfelder, but I’ve also put some thought into how to choose what to research, about whether I could actually be an unmoved mover. A few things get in the way:

First, applying for grants doesn’t just take storytelling skills, it takes scientific knowledge. Grant committees aren’t experts in everything, but they usually send grants to be reviewed by much more appropriate experts. These experts will check if your grant makes sense. In order to make the grant make sense, you have to know enough about the faddish topic to propose something reasonable. You have to keep up with the fad. You have to spend time reading papers, and talking to people in the faddish subfield. This takes work, but also changes your motivation. If you spend time around people excited by an idea, you’ll either get excited too, or be too drained by the dissonance to get any work done.

Second, you can’t change things that much. You still need a plausible story as to how you got from where you are to where you are going.

Third, you need to be a plausible person to do the work. If the committee looks at your CV and sees that you’ve never actually worked on the faddish topic, they’re more likely to give a grant to someone who’s actually worked on it.

Fourth, you have to choose what to do when you hire people. If you never hire any postdocs or students working on the faddish topic, then it will be very obvious that you aren’t trying to research it. If you do hire them, then you’ll be surrounded by people who actually care about the fad, and want your help to understand how to work with it.

Ultimately, to avoid the grant committee’s incentives, you need a golden tongue and a heart of stone, and even then you’ll need to spend some time working on something you think is pointless.

Even if you don’t apply for grants, even if you have a real permanent position or even tenure, you still feel some of these pressures. You’re still surrounded by people who care about particular things, by students and postdocs who need grants and jobs and fellow professors who are confident the mainstream is the right path forward. It takes a lot of strength, and sometimes cruelty, to avoid bowing to that.

So despite the ambiguous rules and lack of oversight, academics still respond to incentives: they can’t just do whatever they feel like. They aren’t bound by shareholders, they aren’t expected to make a profit. But ultimately, the things that do constrain them, expertise and cognitive load, social pressure and compassion for those they mentor, those can be even stronger.

I suspect that those pressures dominate the private sector as well. My guess is that for all that companies think of themselves as trying to maximize profits, the all-too-human motivations we share are more powerful than any corporate governance structure or org chart. But I don’t know yet. Likely, I’ll find out soon.

4 gravitons

Stories about physics from someone who's been there