Science and the malleability of the self

“We still don’t really have any sure answers. We have made so much progress in some spheres, and yet so very little in others. We ought to feel the sting of our own ignorance; beset and bested on all sides by the things we do not know. Why then do so many academics — and applied, business, whatever, “sciency” people — want to act as a colossus, act as if astride the world?”

This is Jessica. Rachael Meager wrote a really great essay last week that ranged over many topics close to my heart (and perhaps the heart of this blog, if it has one), from superficial appeals to rigor and objectivity, heedless acceptance of generalities, disbelief in chance, and a tolerance (or even desire for) breathless predictions with no real mechanism for disincentivizing overconfidence. 

Ultimately it resonated as a meditation on how deep our discomfort runs when it comes to engaging with uncertainty as we construct our little research empires. These are themes that have been on my mind frequently over the last few years. I’d always been interested in limitations of scientific methods but it wasn’t until around the time I got tenure that I felt like I really “dove into the sea of uncertainty and stuck my head in and started blowing bubbles”, to paraphrase a quote from Andrew that Meager also reminded me of. One of the most striking parts of all this was realizing the extent to which people find uncertainty and doubt threatening, even as I was being careful to keep my opinions mostly to myself. It’s almost as if questioning the premises or foundations of certain research threatens the very “personhood” of the researchers involved.

And so, in reading Meager’s post, I found myself thinking about how “avoiding the sting of ignorance” can go hand-in-hand with treating research as a kind of self-affirmation, where scientific investigation gets confused with the unfolding of the scientist’s personal narrative. And counterproductive norms develop to protect the researcher’s right to assert (and preserve) their self through their research.

Meager writes:

Early on in my work I had to contend with people who thought quantitative evidence aggregation was unnecessary or useless in economics; later on some of these same people thought, well, look at the Cochrane handbook, this problem has already been solved. That’s sort of like looking at a stack of bibles and thinking we know everything about god. Actually people wrote the bible, and a lot of those people were fools.

One of the things I find most frustrating when some specific paper or line of work gets criticized as overconfident or unjustified is the seeming unwillingness on the part of the authors to risk something, to stop the knee jerk reaction to find a rationalization and instead actually sit with the possibility that they failed to consider something important. Instead, the fact that their work fits well into some larger landscape of research, where others have asked similar questions using similar methods gets interpreted as a sort of insurance against failing. I remember as a grad student learning that one technique for rebutting critical reviews on a paper you submitted is to find cases where the venue had published other papers that used the same method. Because if they did it and it was acceptable, why should I be held to a higher standard? And so we proceed as if it’s taken for granted that no criticism could ever be so bad as to motivate rescinding the idea.

I think most people do not really believe in inference, for inference means things are hidden. They only believe their own eyes. If something happens they think it obliterates all alternatives. It never could have been a different way. I think that lots of people think the whole world is completely deterministic.

As a result of this, there is enormous pressure to just go along with things. To say, “Okay, it’s fine” when someone presents you with some half-baked result, even after you just explained why you think it is quite far from fine and you don’t see how there is anything that can be said from the results at all. This is not to say that there is never any room for recognizing that the criticism makes a good point–this certainly happens sometimes, and sometimes the critical papers even win awards. It’s more that there is little precedent for truly taking back an idea. Once it’s out there, it must be right. And so once published, even the very bad ideas enjoy a kind of halo that paints them as still somehow valid in some way, and the authors of those papers are still justified in selling them without any real acknowledgement of the limitations. 

Andrew’s analogizing of publication as a kind of truth mill gets at part of this, but I’m interested in the how this arises in part as a result of seeing research as a kind of affirmation of the self. It’s as if we’ve rewritten the definition of scientific learning to be something that stems from ourselves rather than the constraints of the world or of the representational systems that bind us in our particular fields. “Science as a celebration of the self” gets written into how we treat publications and academic milestones like dissertations, even as we claim to be interested only in “objective” truth. Denying that the work is ready gets confused with an attack on one’s right to exist. 

People claim to care a lot about rigour, and exactitude, and chance. But people claim to care about a lot of things.

With chance, in practice, people usually disrespect it. A lot of the time when people say they care about something, they just like the idea of the thing. To respect and to accept something is real is to accept that at times, like all things, it brings challenges. But that is not the way that we normally treat chance.

I was reviewing a paper recently where I was the only reviewer who disagreed with the premise of the work. To me the work was emblematic of how low expectations in this particular field about what constitutes a research contribution have come to validate authors churning out derivative “synthesizing” papers that do some shallow reflecting on trends in some emerging body of literature that was itself ad-hoc and reactive. It was so unambitious, a shot at the “minimum publishable unit”, with no clear generalizable contribution. I tried to get myself to think pragmatically, that maybe this paper was saying something other people would benefit from hearing even if I considered it a waste of time, but I couldn’t find it. And still, among the reviewers, I was the one who appeared to be out of touch. As if the fact that the paper was reasonably well-written and reacting to what had come before meant it was off the table that I could question it in this way. 

This attitude–that those who question the premises or take the holes too seriously must be wrong–is canonized through jokes about R2, the curmudgeonly reviewer who must have some personal affliction if they are trying to shoot down our work. I mean, how can they be justified when the majority of reviewers agreed we were doing fine? Of course we deserve to go to the conferences and have a good time. That’s what we’re entitled to when we submit. If we do happen to get rejected, well, that’s when we believe in randomness and chance. We must have just gotten unlucky. It can’t be that we were wrong.

So on some level it’s not that we never acknowlege uncertainty, it’s that we are only willing to accept it when it’s the wind that blows in the direction of our unfolding personal narrative. The converse of believing that some very hard problem has been “solved” because someone else has worked on it is refusing to accept that there can be a solution or that some real progress has been made, because that would constrain the development of our research identity. I see this a lot in research on research related to human-computer interfaces, whether it’s designing interactive data visualization systems or interfaces to AI/ML models.  For example, I get easily annoyed when people talk about topics like “appropriate reliance” on a predictive model or “evaluating AI explanations,” where often they can provide no clear definition of what they even mean. Meanwhile, decision theory provides a basis for clarifying much of this, but when you present them with such a perspective the response is like, “Well, that is one opinion” and they go right back to letting their intuition drive. 

Or, you point out that a paper already exists that technically solves the problem they care about but they don’t want to acknowledge this, because now that they had the idea that a solution is needed, it must come from them. It’s like we’re very good at pattern matching on the problem, but unwilling to do it on solutions. Once you’ve decided that you want to work on a problem, then it can’t be solved (at least, not by anyone but you). 

The problem is that trying to really learn something new is humbling, especially if you come at it from a position of apparent success. The ego gets built up so, so easily, when things are going well, unless you work hard for it not to. It is not just online writers and clout-chasing posters who mistake numbers or success for importance, or for virtue. It is also real for tenured academics

The ego really does get in the way, and yet, we seem to welcome this. In computer science, we basically train for it. Advancing as a researcher coincides with imposing assertions, rather than learning to listen and slow down and study all of the details before speaking up. We’ve created an academic culture where being confused or at a loss for words has no place. Instead we’re often content to accept vibes in the guise of academic rigor. It’s easier to pretend the ego with its various hopes and dreams really is enough to suss out truth than to try to actually find it. 

And so it’s not necessarily surprising that many trends in how we publish and make hiring and promotion decisions point away from doing deep, thoughtful work, and toward pushing out as many assertions as one can. The expectation that everyone be publishing tens of papers a year, even as a Ph.D. student (at least in certain areas of computer science) is hardly likely to foster deep engagement with uncertainty. Ben Recht has called for less publishing; similar proposals (judge papers based on quality, look at impact) seem to arise every few years since I’ve been a grad student, but so far none of these have made so much as a dent in the hyper-productivity. From the perspective that we’ve created a system with built-in safeguards against any serious threats to the researcher’s sense of self, is there really an alternative? If going deep is too risky, then we’re left with the churn. 

The funny thing is, even in the circumstances where there is the highest premium on being in complete control, like interviews or job talks, often it’s still possible to glimpse that there is an honest human beneath all of the storytelling, who does have a sense of what they don’t know. It’s just that we’ve trained researchers to be extremely cautious about admitting that. Better to pretend that you fully understand it all then to acknowledge in front of others that there’s still some confusion. 

As Meager writes, “there can be a real tradeoff between shooting for (mortal, fleeting) glory and carving out the time and space for good and deep and satisfying work of any kind.”

Ultimately, what one works on, and how much uncertainty one chooses to let in, is a personal decision. The hard part of criticizing researchers for using their work as a form of self-affirmation or self-preservation is that of course we should expect research trajectories to be individualized. Everyone progresses in their thinking at their own rate, in directions that depend on their personal attractions to different topics and insecurities they perceive they must overcome. We become accustomed, even entrenched, in our preferred technical languages or ways of seeing, such that it’s hard to completely blame someone if they refuse to acknowledge a solution in another language, or to relate to doubts raised by someone they see as outside their preferred tradition. Trying to remove the personal entirely from scientific inquiry is unrealistic. 

And yet, I guess part of the sentiment behind this post, which Meager’s excellent essay really got me thinking about, is that as much as “the system” might seem to prevent us from going deep and internalizing doubt, ultimately it’s a personal choice. You can either choose to be the kind of scientist who’s in it for the personal glory or you can let uncertainty in. You can let “the standards” dictate how many papers you write a year and how ambitious each is, or you can try to be honest with yourself about when you’ve learned something worth sharing. There may be no way of omitting the self from science, but there are certainly different ways of using it.