The 1,000 neuron challenge
A competition to design small, efficient neural models might provide new insight into real brains—and perhaps unite disparate modeling efforts.
Today, republishing my column for the Transmitter from 5th of January, with additional commentary by Professor Mark Humphries.
“What can you do with 1,000 neurons?” That’s the challenge driving a competition launched in July by computational neuroscientist Nicolas Rougier. Competitors score points by designing model brains to solve a series of simple tasks inside a maze; the challenge comes from the constraints of using only 1,000 neurons, as well as a training phase of less than 100 seconds in real time and a testing phase comprising only 10 attempts.
Rougier’s competition, dubbed “Braincraft,” moves in a different direction from recent trends in generative artificial intelligence. Commercial large language models have trillions of parameters—and they cost millions of dollars in electricity, processing power and water-cooling to train. Rougier’s focus on small models, by contrast, means that anyone with a laptop (and 100 seconds) can take part.
Rougier’s constraints are inspired by evolution. Lives are short, and brains are energetically costly—something like 20 percent of each individual human’s calories go to maintaining the brain. How to most efficiently derive intelligent behavior from limited energy and limited experience is a defining challenge of biology. “Even LLM models with trillions of parameters could not survive in the real world if you were to provide them with a robotic body,” Rougier says. “In the meantime, the Caenorhabditis elegans, with only 302 neurons, can live a perfect life (of a nematode) in the real world.”
In an era dominated by vast AI models, which bear only the most superficial resemblance to real brains, the Braincraft challenge looks back to nature and asks researchers to put their knowledge of how the brain works to the test. What excites me about the competition is that it helps us explore answers that will be relevant both for understanding the evolution of real brains and for designing more efficient AI.
Competitions of this type have a long history in science. The 1980 “computer tournament” challenged researchers to submit strategies to play the “prisoner’s dilemma” against one another. The winner, surprisingly at the time, was a simple strategy of repeating your opponent’s previous move (“tit for tat”). The results of that competition inspired organizer Robert Axelrod to write his book “The Evolution of Cooperation,” which continues to inform our understanding of evolution.
More recently, a competition called ImageNet galvanized the computer-vision community to compete on image recognition, which has had huge gains during the past decade. In the field of protein-folding, Google DeepMind’s AlphaFold made headlines in 2020 with its success in the CASP competition, which arguably augured the current era of AI.
Rougier was inspired to launch his own competition by a “growing frustration” with the direction of computational neuroscience. “We’ve accumulated an amazing number of models for this or that part of the brain, including cortex, hippocampus, basal ganglia, and yet we do not have a definitive model of any of these structures; we may have something like 1,000 models of V1, but none of them can see,” he says. “The reason lies probably in the way we’re doing modeling, targeting very specific parts without necessarily considering the whole picture.” The competition takes a different tack, requiring entries that combine perception, decision and action in a simple model.
“How to most efficiently derive intelligent behavior from limited energy and limited experience is a defining challenge of biology.”
This logic echoes that of one of the classic papers in cognitive science, “You can’t play 20 questions with nature and win,” published more than 50 years ago by Allen Newell. In that paper, Newell argued that progress would never come from studying individual functions but only from building models that could perform a variety of behaviors. Back in the 1970s, the more radical part of his proposal may have been the emphasis on formal, computational models, but now perhaps it is the emphasis on understanding complete functions. Neuroscience has increasingly specialized in specific areas, model species and functions, adding to the complexity and heterogeneity of our map of the brain.
Rougier hopes that competitions such as his will help put neuroscience back together again. His emphasizes model efficiency. By limiting the number of neurons and the training time, the competition forces winning models to use limited resources more intelligently, rather than wringing performance gains from increased size.
The competition comprises five tasks. As of November, competitors have attempted the first task, and entries are open for the second. The first task asked participants to design a model brain to find a food source located at one of two possible locations inside a maze. The winner used handcrafted weights—fixing specific values for the connections between the sensors and the actions—and just 22 neurons, something that won’t be possible for subsequent, more complex tasks. Third place went to a genetic algorithm, which found an inefficient but ultimately effective strategy of blindly circling the maze. These early results show that simple models employing different approaches can successfully perform simple tasks. But as the competition progresses to tasks that require a broader range of decisions, model-builders will need to explore different strategies for success while keeping their models small.
The competition requires models that can learn to perform complete tasks in an environment, preventing a narrow focus on abstract functions such as visual recognition. Enforcing a limit on training time and model complexity means competitors can’t get complex behavior just by adding model complexity; they have to engage with resource limitations, just as resource limitations were a dominant constraint during the evolution of real brains. Finally, Rougier’s challenge asks people to work on the same problems in a comparable way. Competitors from different theoretical perspectives, or those who favor different modeling approaches, are forced to put their models into a direct comparison.
I’m optimistic that there is a lot that can be learned from this competition, and other neuroscientists share my optimism. “I like the idea of competitions a lot. It provides an opportunity for many people to simultaneously tackle the same problem, subject to the same constraints,” says Anne Churchland, professor of neurobiology at the University of California, Los Angeles. “This is sure to lead to interesting insights.”
Not everyone agrees. Mark Humphries, professor of computational neuroscience at the University of Nottingham, says the competition has a problem with both the format and the alignment of the scientific and competition goals. He is enthusiastic about the idea of competitions in general for driving science forward, citing the success of Axelrod’s competition in the ’80s and more recent image-classification and protein-folding competitions. These examples, he says, offer a formula for the kind of competition that will produce scientific insights. “Successful competitions are accessible to as many people as possible, to bring in a wide range of expertise,” he says. “They have a clear performance target linked to a clear technical goal and repeat so that success and engagement can accumulate.”
Rougier’s competition does have an access bar; competitors must be experienced with both Python and GitHub, as well as have a background in systems neuroscience and neural network modeling, and they have to come to grips with the interface for the competition. A high bar, but perhaps not too rare in the computational neuroscience community.
Beyond that, though, Humphries argues, a scientifically productive competition requires a clear alignment between the scientific goal and the competition task. The image-classification and protein-folding competitions had intrinsically meaningful outcomes—if an algorithm could successfully classify images or predict protein-folding, then the value was undeniable. The 1,000 neuron challenge uses artificial tasks. It is less clear what we’ll learn from the most successful strategies.
A lot rides on whether Rougier has found a sweet spot between the simplicity and artificiality of Axelrod’s competition and the complex and meaningful challenges of recent computer science. Too simplistic a competition would mean that the winner tells us nothing about how real brains solve the challenge of efficiency. Too complex and it will be hard to recruit competitors, and possibly also hard to derive general principles from specific models. Only as the five planned tasks progress will it become clearer if the competition has struck the right balance.
At this point, we also don’t know if the most important thing we’ll learn from the competition is something about the general principles for how to build efficient brains or about how to better design scientific competitions. For certain, though, many—like me—will find the challenge inspiring.
Originally published 2026-01-05 as ‘The 1,000 neuron challenge’ at The Transmitter. https://doi.org/10.53053/OZKJ3100. My thanks to the Transmitter and staff, especially Emily Singer as editor, and to Nicolas, Mark and Anne for speaking to me for the article. Hop over to The Transmitter to get an audio version of this piece, great illustration by Maria Corte, as well as a full range of Neuroscience news and views on many other topics in the field.
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Below other things I’ve been thinking about.
Commentary from Mark Humphries
While I was writing the piece for The Transmitter I contacted Mark for his opinion on the issues brought by the 1,000 Neuron Challenge. Mark is Professor of Computational Neuroscience at the University of Nottingham, a long-term contributor to the Transmitter, author of The Spike: An Epic Journey Through the Brain in 2.1 Seconds from Princeton University Press (2023) and posts essential commentary and reviews of neuroscience research on Medium. So there is nobody better placed to provide expert comment. I thought he’d write me a couple of lines I could quote in the article, but instead he wrote me two pages. It provides a really eloquent critical perspective which I think is worth sharing. With his permission I quote him in full here:
Can competitions help move neuroscience forward?
Competitions have many merits. They encourage innovation by bringing new people to a research problem with fresh perspectives; and can drive rapid improvements from the feedback of your own and others’ performance. Most obvious in recent past are the success of AlexNet in the ImageNet Classification Challenge for, well, classifying images, and AlphaFold in the Critical Assessment of Structure Prediction for protein folding.
Competitions in computational neuroscience have produced few notable successes. I think this is because, unlike ML [Machine Learning]/AI competitions – which are so widespread that dedicated services like Kaggle exist to host them – computational neuroscience problems have a high barrier to entry, often nebulous targets with no clear link to insights into the brain, and happen once. Successful competitions are accessible to as many as possible to bring in a wide range of expertise, have a clear performance target linked to clear technical goal (classify images, protein structure), and repeat so that success and engagement can accumulate
The 1000 Neuron competition is good example of the barrier to entry. Given its time-frame, it ideally requires at the outset strong expertise in coding in Python, the operations of GitHub, of the simulation and use of a recurrent neural network, the training of that network, the interface with a simulated mobile robot, and, given the competition’s aims, some knowledge of systems neuroscience. Few people have those skills; of those that do, fewer have the time to commit to a competition.
A good contrast is with perhaps the most successful computational competition of all, Robert Axelrod’s Iterated Prisoner’s Dilemma tournament. Its barrier to entry was as low as possible: a simple game with easily understandable rules, for which entry was simply an algorithm for choosing your next action – would you choose to betray or cooperate with your opponent in the next round? – and minimal levels of coding needed. Axelrod directly approached a wide range of experts to solicit their entries. Famously the winner was Tit-for-Tat, which simply chose whatever your opponent did to you last time; yet this simplicity spawned deep insights into social cooperation among members of the same species, and insights from this competition are still driving research today.
For me, the most successful use of competitions in neuroscience are closer to the AI/ML format, with a well-defined, simple technical goal, around which a range of expert teams can compete. A good example was Philipp Berens “spikefinder” challenge in 2018, which tasked teams with finding the true spike rates underlying calcium imaging signals recorded from a variety of neurons, seeking to drive the development of new algorithms for recovering spiking activity from slow calcium signals.
One strength of competitions like spikefinder and the 1000 Neuron Project is that they encourage people to adopt the same benchmark, a set of evaluations that enable direct comparison of solutions, and their performance, strengths and weaknesses. The 1000 Neuron Project rightly points out that one thing holding computational neuroscience back is that models are not evaluated on the same challenges and so cannot be compared. Others have tried to solve this by developing standardised task sets for neuro-inspired recurrent network models to solve.
Will we learn anything from the process?
It’s unclear that we will. The scientific goal is to go beyond engineered models of specific brain circuits and construct a mini-brain for control of continuous performance. The performance goal is to maximise distance travelled, by a simulated 2D bot using a generic Echo-State Network. The two goals are not clearly related. I suspect that solutions for optimising the performance goal will tell us little about how the brain solves such problems. A good analogy is the problem of self-localisation: in the mammalian brain, we know the complex circuit of the hippocampal formation and the head direction system implement this function; but given a performance goal of self-localisation the answer is one of many state-of-the-art Simultaneous Localisation and Mapping (SLAM) algorithms from control engineering and robotics, that have no neural constraints, and most of which tell us nothing about the brain. But predicting the future is folly, for who knows what might serendipitously emerge?
The one thing I would argue is that we’re most likely to learn from competitions that repeat. Both AlexNext and AlphaFold were entries in to long-running competitions. It can take some time for new people to commit, new ideas to emerge.
What kind of approach do you predict will be most successful? Do you have any advice for competitors?
The kind of problem posed in the 1000 Neuron Challenge, of an embodied agent surviving in a 2D world, has a long history in AI research, stretching back to the start of the Artificial Life movement. Historically, Evolutionary Algorithms were used to winnow agents equipped with a range of neural networks coupled to RL [Reinforcement Learning] systems. It would seem an approach of a similar spirit would be needed for this challenge, as there are two time-scales of learning to worry about: in the short-term, where the source of energy is on this particular run; and in the long-term, the possible locations it can take across runs. It need not be, of course, two separate learning approaches.
Other things..
When Cheap Signals Flood the Market, Costly Signals Appreciate
Relevant to last week’s newsletter When trusted signals collapse, part of a sequence on signalling theory (part #1, part #2):
When cheap signals flood the market, economic logic predicts a flight to costlier, harder-to-fake signals. A degree from a reputable institution—earned over years under structured evaluation—remains relatively expensive and difficult to counterfeit. Simply put, one would expect that if AI makes short-run competence easier to mimic, employers lean more heavily on long-run indicators of reliability. Not every institution benefits from this dynamic, but it may help high-trust universities, and hurts low-trust institutions.
Jimmy Alfonso Licon: AI May, Paradoxically, Increase Demand for Higher Ed
…and finally
From J. L. Westover
Comments? Feedback? Brother can you spare a neuron? I am tom@idiolect.org.uk and on Mastodon at @tomstafford@mastodon.online
AI declaration: I write all the words and think all the thoughts myself. I usually ask Gemini to check for spelling and grammar, but for this piece I didn’t even do that because I had editorial support from The Transmitter.