What happens when research is "done"?

by Kent Lyons, May '22

Living in research, there is a lot of time devoted to coming up with the next research project, executing on that work, iterating based on early insights, etc. But what happens to the research when it is done? Who is going to consume the results? Well the easiest answer is that the research is published when it is done (maybe after a few tries and a few more iterations). At that point it is launched off into the world and becomes part of the larger academic discussion. With luck it becomes a meaningful part of the dialog, teaching people something new and being the seed for future work. So the consumer is the amorphous academic community at large. If that happens (or not) is largely outside of the researcher's direct control once things are finished. (With the exception of things like picking the right topic up front, and promoting the work afterwards). It's also possible that one piece of research is part of a larger body of work, be it a Ph.D. dissertation, or a step called out in a funded grant. Here, one set of research feeds into the next and the researchers themselves are the consumer.

What if we are interested in carrying the work farther into the real world? In that case, the work is not "done" when the paper is finished. However what does need to happen next? Either the work needs to be folded into an existing product/business or a new one needs to be created. The consumer of the research is some sort of business entity, existing or new. (There is also a path that uses the research to influence policy, but I'm not focusing on that here). This transition points to well known problems like needing to bridge the valley of death. However if that is the end goal, we can work backwards to understand which kinds of research might have better success following such a path, or conversely which research might find that path harder for a given context.

As I think about the work we do at Inovo Studio, this is a central question and I can't help but think about an associated research life cycle from inception to deployment. I've lived most of my career in a corporate research setting (with a stint at my own startup and some time on product as well). These research organizations have all had various mechanisms in place for proposing and executing on ideas. Some of them are much more formal, others more ad hoc. A couple of them had their roots in DARPA, including the Toyota Research Institute where I was before starting Inovo Studio. DARPA has a lot of history and culture. And while I worked closely with senior leadership at TRI who had that DARPA background in building up our new department and its research agenda, it was clear I was only touching upon the surface of the institutional knowledge representing the DARPA approach.

A topic that came up numerous times was Use Inspired Basic Research and Pasteur's quadrant. One of the key ideas with this framing is that instead of placing research on a single dimension between basic and applied, there are two dimensions. One is about a quest for basic understanding (or not) and the other dimension is around considerations of use - what are the results of the research to be used for? The classic example of no quest for fundamental understanding and a high consideration for use is Edison. He didn't care why the light bulb worked so long as it did. At the opposite corner is Bohr and his desire to understand atomic physics with little concern as to how that knowledge might be applied. The use inspired basic research quadrant is exemplified by Pasteur who both wanted to understand the underlying issues of microbiology he was studying, but also apply those leanings into things like his namesake, pasteurization.

Overall I like this framing, but as alluded to above, there is also a lot of nuance coming out of it's DARPA origins, particularly around the notion of use. I have a hunch that there are some key differences between DARPA, being a government organization tasked with developing new technologies for the military, and industrial research. One such difference is about the nature of the problems to be solved and for whom. And central to this discussion, once those problems are solved with research findings, how resources are deployed to put those solutions into practice. In other words, who is consuming the research and how are they acting upon it?

In a company, the problems to be solved are really dictated by the market - the company's customers. It's the customers who vote with their dollars to decide if a solution is valuable or not. From a use inspired perspective, at least at a superficial level, the uses are relatively easy to understand. There is a lot of knowledge built up in the organization and its customers about what the product does and what it might mean to be better. Use inspired research then would be making that better in some way. (We can also consider research on improvements to the business process itself, eg making things cheaper, using a new/better material, etc. Here the customer shifts from an external one to an internal one, but otherwise much is the same. There are current uses/problems in place and the improvements are seen and judged in light of those). As soon as we dig a bit deeper, we also find that there are also significant organizational investments into the approaches used to solve that problem for the customer. And likewise, expectations from the customer as to how their problem is solved with that product.

To be a bit more specific, let's make up an example. Imagine a company is manufacturing dog food. Clearly that is the product and the problem to be solved is a bunch of hungry dogs. This company's main ingredient for its dog food are grains and it adds in various other ingredients to make a healthy food for dogs. One day, a new process is invented that uses genetically engineered yeast that drastically reduces costs. The yeast is grown and produces a complete food for the dogs without any additional processing steps and requiring fewer raw ingredients compared to the traditional method. The yeast only needs to be grown, dried and compressed into the final dog food. The researchers are very excited since this is clearly a better way to produce the product. The use for this research, producing dog food, seems well aligned with business needs.

Unfortunately the company is less enthusiastic. It doesn't have any of the capabilities to grow these yeast: it would need different equipment, different suppliers, different skilled labor. What this really requires is standing up a full new business. If the resulting dog food is exactly the same, then the only thing that might stay the same is the sales channel and customer. However if the dog food itself is different, then there is also work to be done getting the customer on board. Now it is possible that the company might stand up that new business, almost none of the employees in the company have that capability. They are all devoted to the current process. It would take significant intervention from senior management to create such a new business. There are also significant costs and risks to go down this path, and most well established companies tend to be rather risk averse even if they understand the possible benefits.

Well, a startup sees this new technology, and it has no legacy infrastructure so decides to give it a go. It is indeed a better way to make dog food. Over time the startup grows and eats the market share of the incumbent. Maybe the incumbent buys the startup and pivots. Or maybe it's too late, and the startup can just keep going and become dominant. The use for the yeast based dog food seemed aligned with the companies need, but the nature of the research results could not be consumed by that business. It required a new business to actually take those results forward.

I'm no expert, but I think in the world of DARPA is rather different than this one. DARPA funds a way to make better dog food. It scales up the research, and as it becomes promising, DARPA, with its military partners, puts out a bid to the military-industrial-dog-food complex to fulfill the new dog food supply contract. Some of the previous suppliers might have the incentive to pivot and build up the new process. Others probably go down. However, DARPA and it's military partners are not particularly concerned with the health of any one of those business as along as it can find a suppler. These dynamics seem very different than in a corporate setting. DARPA is able to move the market in a way that doesn't seem to happen in the private sector. (If you know more about this world and I'm getting it wrong in some critical way do reach out - I'd love to chat more).

Returning to the use inspired basic research framing, the new yeast research seems well aligned with the notion of use, the problems the business is trying to solve for its customers. This is as seen from a macro perspective of the overall value chain. However, as soon as we look at the current business, this breaks down. The problems the current business sees are relative to how the product is currently being produced. For example, how might the business incrementally improve what it is currently doing to produce a better product more efficiently (not replace the process all together!)

So while the use might be aligned in theory, in practice there is a rather large disconnect. A similar problem can happen at a more local scale. Taking a human computer interaction perspective, one of the challenges of better understanding one's users is in listening to their feedback about some software. There is an art to tease out what might be underlying problems users are encountering from more superficial issues. Just because a users says then need XYZ, does not mean it would actually be used or help if XYZ magically showed up. Or similarly, it is important to disentangle symptoms of a problem they face from the underlying causes. Ideally we can fix the causes instead of just treating symptoms.

If we consider possible uses in a business context, we face a similar challenge. The business unit will talk about the fires they're fighting today, or the flavor of the week in terms of possible direction. One needs to dig deeper to know what might be of more fundamental value (especially considering research will likely land much farther into the future than the business unit is thinking). Once those deeper problems are really understood, one can build a research program and possible technological solutions for them. However the results, the resulting research, might hit similar impedance mismatches. To apply that research might also require changing the business practices in some way so it can be adopted, or even harder, the organization around it. Maybe the technology is a drop in replacement or addition for some core problem of the business. However given the need for research and more significant innovations, that seems rather unlikely and instead other things would need to change as well.

In a business setting, we need to think not only about the considerations of use, but also who might consume that research and what processes they already have in place. So as we embark on a new research idea, if the end goal is eventually to transition it into the world in the form of product, we need to think about this pipeline from research inception, through execution, and critically here, to consumption of the research results. Some research might align much more naturally with its consumer. Others might be farther afield. Maybe the research solves the same fundamental issues, but in a radically different way. Or maybe the research takes some core competencies and applies them to a new problem. Given this landscape, we can bias ourselves towards possible success (or avoid likely failure) by thinking not only about the research and the novel ideas behind it; but more fundamentally the pipeline after the research and what consumption of that research might look like.

I should also note that this is assuming the core business is largely immutable. I've alluded to some of the reasons this is the case above, and will dive into it in more detail in future articles. Businesses can change, but researchers are not really in the position to induce such changes (beyond championing their results). Even senior management, who sponsored and supports the research and associated changes, might have an uphill battle shifting the organization.

For Inovo Studio, the potential use and adoption of research results are front and center since our goal is to take promising research and see if we can move some of it into the market. But I think it is a worthwhile effort to think about the paths for research after it is "done" in academic and industrial research settings broadly as well. Who is going to consume the research (assuming it works)? What will they do with it? Does this (closely) align with how their world currently works (this is often a critical point of failure where the researchers make some assumptions that really are not valid)? Even what appear to be small changes can be hard in a larger organization with all sorts of legacy and interdependencies. In a corporate setting these things might be possible. And they may fall under an umbrella of "tech transfer" but the research and associated technology might be the easy part. It's the organizational and business changes that are hard and require significant resources. Another path is to bypass the legacy and to spin up something new. This is hard in a different way - proving product market fit - but at least there are not the uphill organizational challenges in place. And this is the path Inovo Studio is taking.