Thinking about brain research this way is a bit of a twist on how we normally think about things. I would say that we tend to think more in terms of findings, eg "That paper found ..." whereas this is something more like, "That stack of papers is working on the idea that ..."

It's interesting to think about one's own work in that light: What ideas am I working on and who else is working on the same idea (perhaps with a different approach)? Similarly, what sorts of ideas is the field working on? And are these ideas new or old?

Here's a slightly more provocative way to pose the question: In The Idea of the Brain, Matthew Cobb argues, "In reality, no major conceptual innovation has been made in our overall understanding of how the brain works for over half a century ... we still think about brains in the way our scientific grandparents did."

Setting aside semantic debates about what constitutes a "major conceptual innovation", brain researchers are clearly working on a large number of ideas that their grandparents had not thought of. But what are those, exactly?

@albertcardona @matthewcobb

Or this one? Across different individuals, the same brain functions are implemented by biological details that vary a lot. This is true even for simple circuits like the ones that control the stomach of a crab, where the numbers of ion channels can vary 2-6x across different crabs but the circuit always does the same thing.

https://www.sciencedirect.com/science/arti

@NicoleCRust @albertcardona @matthewcobb
One of the things I've been struggling with recently is how the vast majority of papers (including most or arguably all of mine) don't propose an idea that could in principle get us closer to understanding how the brain does what it does. I have the feeling that there was this moment in time when people were coming up with tons of crazy theories. They were all wrong (probably) but it was exciting. Now we're just talking about how many dimensions a 'neural manifold' has and I just can't get excited about that (sorry manifold people). In my case, I think I've had a small handful of ideas that went in the direction I'd like neuroscience to be going in of proposing ideas that could scale to part of a full explanation of the brain, but I haven't pursued them because they were hard to define or get funding for. My resolution for 2023 is to focus more on those interesting questions and less on things that I think are easy to get published or get funding. For what it's worth, the biggest challenge to neuroscience I reckon is how it can operate in a stable way based on what seems to be a surprisingly unstable substrate (e.g. synaptic turnover). If I had a good idea about how to solve that problem, that's what I'd be working on.

Edited to add: I don't mean to criticise anyone's work! It's more a personal realisation that I've not been pursuing research directions that I believe could really lead to understanding the brain. On a metascience level, I think it's important that different people take very different approaches, most of which they will disagree on. If it's not like this, we won't make progress. My realisation is perhaps that I've been trying too hard to fit in and it's not working for me.

@neuralreckoning
@NicoleCRust @albertcardona @matthewcobb @WiringtheBrain

Dan, I'm not sure I agree with you but need to think. One place for ideas is in review/conceptual papers and I think there's a good amount of ideas going around in those. I have tried to be active on this end, or at least as much as time permits.

@PessoaBrain @neuralreckoning @WorldImagining @NicoleCRust @albertcardona @matthewcobb @WiringtheBrain A latent question throughout this thread is whether we would recognize a powerful new idea if it did come along (or has come along?...). It seems common to expect "new" ideas to be "exciting", etc, but I don't see those expectations as necessary or even desirable. If some new concept is a stepping stone to a powerful shift in understanding, it seems just as likely it would be difficult to reconcile with our current way of thinking. Otherwise, why didn't the shift already happen?

A really new idea about the brain is likely to be challenging and unreasonable, to be something we instinctively try to reject. More a thief in the night than a triumphal entrance, waiting for its importance to be discovered in retrospect. Like the old joke: every great scientific idea is wrong before it is obvious.

I expect you have counter-examples to offer, and I am dramatizing a bit. But a paltry return on the enormous number of person-hours going into brain science might arise not because we just haven't found that great new idea yet, but because we're fundamentally wrong about something, and error correction is psychologically harder than novelty detection.