Connectionists: Building a healthy theoretical neuroscience community

[Randall O'Reilly]

To pick up on this thread of the discussion:

* If we want to build a healthy and vibrant community, we need to be supportive of a plurality of research approaches — there are sub-fields of science where everyone is supportive and constructive, and these fields get their papers published in top journals, and cited widely, and grants funded, etc.  Then there are fields where everyone is cutting down everything that is “NIH” (not invented here).  Those fields are suicidal.  Perhaps because of the creative nature of the modeling process, people tend to get strongly attached to their creations, and mistakenly view other ideas as threatening.  If there are multiple clear, sensible alternative models, with distinct testable predictions, then we are contributing productively to the larger field, and almost every experimentalist I’ve ever talked with is excited by that kind of thing.  Along these lines, I personally have made a strong conscious effort to be as constructive and positive about papers that I also have strong concerns about, including one that was discussed earlier in this thread.  The more theoretical modeling papers that are published in high-profile journals, the better — we really do all win when any one of us is making an impact!  [Obviously, you don’t want to suspend all criticism, and you don’t want obviously bad stuff to be published, but you really do have to work hard to distinguish opinion from quality..]

* The perception expressed in several comments that theoretical work is not impactful rings false to me, and sends an overly pessimistic message and “negative self image”, which is also not constructive to building a growing and vibrant community.  I can point to a large number of domains where computational models have played central roles in shaping the broader theoretical discourse and experiments, including in the hippocampus, basal ganglia & dopamine reinforcement learning, prefrontal cortex, and in visual object recognition (and probably a lot of other areas I don’t know enough about). The recent work on grid cells in the entorhinal cortex is a spectacular example of the interplay between models and experiments, for example.

* Also, whoever thinks the BRAIN initiative is draining resources is crazy.  It is a TINY amount of $ relative to overall budgets, and furthermore all the recent DARPA initiative teams (which represent roughly $100 million I think) that I know about involved a major contribution from theoretical / computational modeling.  More generally, various branches of the DOD and intelligence research communities, and obviously industry such as google etc, are increasingly optimistic about brain-inspired approaches to intelligence, so this is an incredible opportunity for growing our field.  And from what I’ve seen, there is an strong recognition among those in charge of giving out the $ that this is *the* hard problem, and it will take a sustained investment to make progress, but there is enough promise already that these investments are clearly going to pay off.  So we should be breaking out the champagne, not spewing the sour grapes!  I would be doing so if I wasn’t so busy writing so many damn grant proposals! :)

- Randy

On Jan 26, 2014, at 12:43 PM, Geoffrey Hinton <geoffrey.hinton at gmail.com> wrote:

> I can no longer resist making one point. 
> 
> A lot of the discussion is about telling other people what they should NOT be doing. I think people should just get on and do whatever they think might work.  Obviously they will focus on approaches that make use of their particular skills. We won't know until afterwards which approaches led to major progress and which were dead ends. Maybe a fruitful approach is to  model every connection in a piece of retina in order to distinguish between detailed theories of how cells get to be direction selective. Maybe its building huge and very artificial neural nets that are much better than other approaches at some difficult task.  Probably its both of these and many others too. The way to really slow down the expected rate of progress in understanding how the brain works is to insist that there is one right approach and nearly all the money should go to that approach.  
> 
> Geoff
> 
> 
> 
> On Sat, Jan 25, 2014 at 3:00 PM, Brad Wyble <bwyble at gmail.com> wrote:
> I am extremely pleased to see such vibrant discussion here and my thanks to Juyang for getting the ball rolling.
> 
> Jim, I appreciate  your comments and I agree in large measure, but I have always disagreed with you as regards the necessity of simulating everything down to a lowest common denominator .  Like you, I enjoy drawing lessons from the history of other disciplines, but unlike you, I don't think the analogy between neuroscience and physics is all that clear cut.  The two fields deal with vastly different levels of complexity and therefore I don't think it should be expected that they will (or should) follow the same trajectory.  
> 
> To take your Purkinje cell example, I imagine that there are those who view any such model that lacks an explicit simulation of the RNA as being incomplete.  To such a person, your models would also be unfit for the literature. So would we then change the standards such that no model can be published unless it includes an explicit simulation of the RNA?  And why stop there?  Where does it end?  In my opinion, we can't make effective progress in this field if everyone is bound to the molecular level.  
> 
> I really think that neuroscience presents a fundamental challenge that is not present in physics, which is that progress can only occur when theory is developed at different levels of abstraction that overlap with one another.  The challenge is not how to force everyone to operate at the same level of formal specificity, but how to allow effective communication between researchers operating at different levels.  
> 
> In aid of meeting this challenge, I think that our field should take more inspiration from engineering, a  model-based discipline that already has to work simultaneously at many different scales of complexity and abstraction. 
> 
> 
> Best, 
> Brad Wyble