Involuntary collaboration: a strategy for decentralized science

How your best co-worker, might be someone you’ll never meet

In most organizations, ranging from startups to academic labs to large companies, the person with whom you work most closely might be someone in the same building, or working under the same boss, or in the same hiring cohort. But what if you structured your work so that your best co-worker might be someone anywhere in the world? Maybe someone you’ve never met? Maybe someone you will never meet? And yet, by working together, you could make something amazing happen - perhaps something neither of you could have imagined, working alone.

In the realm of science, people often talk about Bell Labs, in the 20th century, as a vanguard of innovation, having developed the transistor, the laser, the solar cell, information theory… the list goes on and on. One of the reasons given for Bell Labs’ success was its ability to foster collaboration, maximizing collisions between people in its legendary cafeteria, and encouraging people to keep their doors open. The Bell Labs model worked well for a vast number of 20th century problems. But what about 21st century problems, which often seem to be of much greater complexity? Many of these problems are “network problems” - problems involving complex systems, made out of many building blocks, which interact in complex ways, making it hard to study or fix such systems. Such problems can be overwhelming when treated reductionistically (people often resort to focusing on an ultra-narrow hypothesis in a vast sea of possibilities), yet too approximative when treated phenomenologically (which discards mechanistic detail and results in nonrobust conclusions). Biology and medicine are full of such problems. Can we design a collaborative framework to facilitate great innovations, in such fields?

Let’s examine how great biological and medical inventions and discoveries arose in the past, and see if patterns emerge. If they do, then perhaps we can create learnable, teachable versions of those patterns - aiming to do on purpose, what previous generations did by accident. One observation is that many great biological innovations arose because of different people who contributed unique and independent insights, often over an extended period of time. This observation may sound trivial, but it’s worth exploring how it might guide us to proactively choose our behavior. As one example, take the green fluorescent protein (GFP), which was discovered in a species of jellyfish by a marine biologist in the early 1960s. The gene was then isolated and proposed as a tool - namely, to enable cells, or specific proteins within cells, to glow green, so that they could be tracked under a microscope - by a molecular biologist in 1992. The gene product was shown to work in living cells, by a neuroscientist, in 1994. The protein was made brighter, and mutated to form more colors (e.g., yellow, cyan), by a chemist in the mid-to-late 1990s. In 1999, red fluorescent proteins were discovered, in corals, by another team. In each case, the person or people involved worked at a different institution than the others, and sometimes were even from different fields than the others. Furthermore, the work was done over a period of decades. Today, millions of studies have benefited from using fluorescent proteins to tag cells, and proteins within them, to follow them over time.

As a second example, take CRISPR, which revolutionized genome editing, and is being explored for correcting disease-causing mutations in humans. The original characteristic DNA sequence of CRISPR was discovered accidentally by a molecular biologist in 1987. Around 2005, the protein Cas9, which performs the enzymatic action associated with CRISPR, was first described and identified as a nuclease protein. In 2007, scientists studying bacteria relevant to yogurt manufacture showed that the CRISPR system could help bacteria defend against viruses. In 2012, researchers showed that you could use the Cas9 protein and a specific accessory known as a guide RNA to cut a targeted piece of DNA, demonstrating the programmability of the system. And in 2013, scientists showed that such genome editing could be done in a living human cell. (As with any scientific discovery, there were several other critical steps not mentioned here, key to the ultimate success of the discovery; our goal in this essay was simply to illustrate the distributed nature of discovery, and not to provide a comprehensive history.) Again, people working at different institutions, and approaching the problem from different fields, working over a period of many years, were key to making CRISPR useful.

As a final example, let’s take the case of GLP-1 drugs, which are sweeping the headlines as they help human patients with diabetes, obesity, and other problems. The peptide GLP-1 was discovered in 1986, and its effects on metabolism characterized throughout the late 1980s and beyond. But the natural peptide has a very short half-life in the body, making it difficult to use as a drug. In the early 1990s, work on Gila monster venom, of all things, revealed GLP-1-like molecules that could last longer in the body - long enough to make for a meaningful drug. In the mid-2000s, GLP-1 agonists with ever-increasing efficacy received FDA approval, and by the mid 2010s to early 2020s, easy-to-administer forms, that last for very long durations, went mainstream in medicine. Again, different steps were achieved by different experts, working at different places, and over a long period of time.

Could any of these biology achievements have been conducted under one roof, by a fixed set of people? It is hard to see how. In short, the Bell Labs of the 21st century is the whole earth. In such a situation, how should you structure your work? For the purposes of today’s article, we’ll stick with biology, but one can perhaps imagine similar strategies applying to other 21st century problems (the success of open source software endeavors, such as the Linux operating system, comes to mind).

In biology, people often perceive a dichotomy between basic science, driven by curiosity, but often of unclear application, vs. translational work, driven by a medical or application goal, but sometimes exhibiting high risk (e.g., clinical trials are expensive and have a high failure rate). Both kinds of science, of course, are important. What if, as a third path, one could invent a tool that enables many biologists to go after basic science discoveries, perhaps ground truth-oriented ones (i.e., focused on fundamental building blocks and their interactions), deploying it freely to the community? Those scientists can apply the tool to different kinds of problems, making foundational and mechanistic discoveries. Then, one can design a translationally optimal implementation of a particularly interesting discovery, to solve a long-felt need. This “invent, deploy, discover, design” (or ID³ for short) strategy may be useful, when approaching a complex problem space. It’s a way to form involuntary collaborations, simply because the incentives are aligned - people will work together, even if they never meet, to tackle a problem space systematically.

Let’s consider an example of such an ID³ project: optogenetics. In optogenetics¹ (“opto” for light, and “genetics” because the technology is genetically encoded), we control the electrical activity of brain cells, or neurons, with light. By activating the electrical activity of specific neurons, say in a mouse, we can see what behaviors, or pathologies, or therapeutic states, they might cause. By silencing the electrical activity of specific brain cells, we can see what behaviors, or pathologies, or therapeutic states, they are needed for. We achieve this by borrowing proteins from the natural world, that normally convert sunlight into electrical current in single celled microbes. Such microbial rhodopsins (which were discovered starting around 1971, with many distinct classes being reported over the decades following) are used by organisms either to store solar energy in chemical form, or to navigate around bodies of water for optimal photosynthesis.

In the year 2000, one of us (Ed) along with a fellow student decided to try to use these microbial rhodopsins to mediate the optical control of neural electrical activity. In 2005, we published the first report on using a specific microbial rhodopsin from single-celled green algae, to make neurons activatable by pulses of blue light (the invent phase). We disseminated the molecule freely, to thousands of scientific research groups (deploy, with great help from the nonprofit DNA-distributing service Addgene²), and people started applying the molecule to a diversity of scientific problems (discover). Importantly, optogenetics was easy for people to use, which helped the technology spread widely. We, and others, found more and more microbial rhodopsins, with different properties. One group in Europe was trying out optogenetic molecules in the retina, desiring to to treat forms of blindness in which photoreceptor cells die, like retinitis pigmentosa. The core idea was to make cells of the retina which did not die, into artificial photoreceptors, by equipping them with rhodopsins. We helped them figure out which molecule to use (design). In 2021, the European team reported that this molecule could be expressed in the retina of a blind patient with retinitis pigmentosa, and helped him achieve a partial restoration of functional vision. Clinical trials are now being conducted by many companies, of such optogenetic tools, in the context of blindness.

Another collaborative set of groups, in 2009, used an optogenetic molecule to discover neurons that, when activated in the mouse brain, caused brain circuits to undergo electrical oscillations, or brainwaves, preferentially at a gamma (~40 Hz) frequency. In 2016, one of the groups collaborated with our group to find that stimulating such brainwaves in Alzheimer’s model mice (i.e., mice engineered to get Alzheimer’s-like symptoms) caused the brain to clean up its molecular pathology. Later, that group, collaborating with our group and other groups, designed flickering lights and clicking sounds that, because they ran at 40 Hz, could clean up the molecular pathology of Alzheimer’s, and improve cognition, in mouse models (2016-2019; note that optogenetics was no longer needed). Now, human trials are underway with Alzheimer’s patients, with a startup company co-founded by the group leaders (including one of us (Ed)) aiming for FDA approval. Small-scale trials have shown promise in slowing the progression of Alzheimer’s. By following ID³ we facilitated multiple discoveries with practical implications for human health, that we would have probably never solved on our own.

Let us pick a second example - expansion microscopy (ExM)³. In ExM, a preserved biological specimen is chemically permeated by a dense mesh of swellable polymer - basically, the active ingredient in baby diapers. Adding water to such a polymer-embedded specimen causes it to swell by ~10x or more, in linear dimension. Such samples can then be imaged with nanoscale precision on ordinary microscopes (which are otherwise limited in resolution to about 300 nanometers or so, perhaps 100x bigger than a biomolecule). Our lab announced ExM in 2015 (invent), and quickly people started to learn it from our papers, websites, and protocols (deploy). After all, the building blocks of life are nanoscale, and interact over nanoscale distances, so there was much pent-up demand for an easy-to-use nanoimaging technology. At the time of writing of this article, perhaps 800 experimental studies have appeared using ExM - many discoveries have been made with ExM. And, as with optogenetics, ExM is easy to use (one ExM pioneer announced⁴, “It’s so easy, even my nine-year-old can do it”). Interestingly, as the discoveries flowed, people started modifying and adapting ExM for their own purposes, sometimes working with us. As just a couple examples of this (design) - in 2024, a group announced that they could expand fragments of a protein away from each other, evenly, so that you could see the shape of the protein on a light microscope - quite a surprising outcome. In 2025, another group announced they could break the genome, while still inside a cell, into pieces, expand the pieces away from each other, and then sequence them - enabling nanoscale visualization of both genome sequence and structure, while still inside a cell. Finally, in 2025, two of our group’s alumni, now running their own labs, led the way on a project to expand the whole body - bones and all - by adding in a softening step for bone, before the expansion step began. ExM benefited from the fact that ExM was not only easy for others to apply, but also easy for others to improve - in other words, there was a bit of an “ID³ chain reaction” here, where a design step could also serve as an invent step, triggering another round of innovation.

In short, ID³ might be a good model, for many kinds of scientific problem where you want to achieve a practical outcome, without losing sight of underlying ground truth. One key insight is that ID³ reduces risk by having many people work on the middle discover step, using technology that has been deployed to them. Of course, for this to happen, an invention must be easily applied, and ideally inexpensive. A technology that is not easy to use, may not be amenable to this model. (For those of you who have read the book “The Innovator’s Dilemma,” which discusses how new startups can disrupt industries ruled by old companies, there might be parallels: ID³ might be a sort of scientific cousin of that idea.) Another reason ID³ works well is that collaborating too actively might sometimes be bad for innovation: if experts work too closely together, they might not give a risky idea generated by one of them, a safe space to grow: perhaps some of the other experts might judge it to be infeasible, according to established but inaccurate, or outdated, dogma. Rather, sometimes you need a “skunk works” where a team can work on an idea without being told by others (e.g., upstream inventors, downstream designers), that their idea is stupid. There is a certain kind of strategic ignorance that can help with serendipity - you don’t know that something is impossible, so you give it a try anyway - and because the experts were wrong, you succeed. Finally, ID³ helps increase the number of stakeholders who want to see a technology succeed. They can find many applications of it to different problems. They can support each other, sharing wisdom. By sharing ownership of a technology with many, it can become “too big to fail” and take on a life of its own. From the tool inventor’s point of view - there is an opportunity cost if they stop invention, and instead switch to application. If a tool inventor pursues one application, out of 1000 possibilities, and that application fails - that could result in far less impact than if they simply gave the tool to 1000 people to pursue those 1000 possibilities, some of which may prove revolutionary, even if most fail.

Can we create a system, sort of a decentralized worldwide Bell Labs, to achieve ID³ at scale? Imagine an organization that could help define problems, facilitate invention of tools, orchestrate deployment of technology, nurture discoveries, and help with the design phase - all in a completely globally distributed fashion. Perhaps this organization could identify appropriate people to tackle different tasks, rapidly allocate funding and other resources to them, and upon project completion, allocate credit and reward appropriately. In contrast, current incentive structures are not necessarily a great match for ID³. A group might hold back on publishing a tool, hoping to make a big discovery on their own, rather than deploying it - depriving the world of the tool. The ID³ process can take years, and sustained activity in science is challenging, as any one advance might seem incremental, and thus unappreciated. (Many of the stories above encountered such bumps in the road along the way - optogenetics was a hard sell, and resulted in one of us (Ed) struggling to find a job⁵, and expansion microscopy struggled to get funding⁶.) Much of the credit, and/or profit, may go to the people who take the final step, with the initial steps being hard to fund (because they are so remote from the value, which only becomes apparent after the final step is taken), and hard to attribute credit for (for similar reasons).

Perhaps a blockchain-like structure could help - tracking all the value generated, from initial invention, to later deployment and discovery, to final design, routing resources to those who could make contributions, and helping assign rewards to them later - perhaps when their work might have been otherwise forgotten, because the latter steps captured perceived value and obscured key initial steps. If the profits from a successful therapeutic, for example, could flow upstream to those who made enabling discoveries, and the inventors of the tools who empowered those discoveries, perhaps that would align the incentives of biology better. As a special case, right now there might not be much incentive for people to publish negative results. But if someone were to put a negative result on the blockchain, and when someone uses the information later for a successful project, a portion of the reward could flow upstream to the originators of the negative result that helped the later project head in the right direction, that could be beneficial to all. For this to work, access to the blockchain of knowledge would require some kind of enforceable agreement about sharing of future credit and profits. But perhaps someone could figure that out.

In short, involuntary collaboration allows for innovation to flourish, and perhaps there is a way to perform it, consciously and deliberately. There’s an old saying, if you want to go fast, go alone. If you want to go far, go together. Here is a way to do both.

1. https://www.ted.com/talks/ed_boyden_a_light_switch_for_neurons?language=en

2. https://www.addgene.org/

3. https://www.ted.com/talks/ed_boyden_a_new_way_to_study_the_brain_s_invisible_secrets?language=en

4. https://doi.org/10.1038/d41586-025-00059-6

5. https://engineeringx.substack.com/p/engineering-serendipity

6. https://www.openphilanthropy.org/grants/massachusetts-institute-of-technology-synthetic-neurobiology-group/