Reflection on Robotics and Application Science Research

TL;DR: Application science fields like robotics need to be more rooted in real-world problems. Furthermore, instead of mindlessly working on their advisors’ grants, PhD students may want to spend more time to find problems they truly care about, in order to deliver impactful works and have a fulfilling 5 years (assuming you graduate on time), if they can.

What is application science?

I first heard about the phrase “Application Science” from my undergraduate research mentor. She is an accomplished roboticist and leading figure in the Cornell robotics community. I couldn’t remember our exact conversation but I was struck by her phrase “Application Science”.

I have heard of natural science, social science, applied science, but never the phrase application science. Google the phrase and it doesn’t give much results either.

Natural science focuses on the discovery of the underlying laws of nature. Social science uses scientific methods to study how people interact with each other. Applied science considers the use of scientific discovery for practical goals. But what is an application science? On the surface it sounds quite similar to applied science, but is it really?

Mental model for science and technology

Recently I have been reading The Nature of Technology by W. Brian Arthur. He identifies three unique aspects of technology. First, technologies are combinations; second, each subcomponent of a technology is a technology in and of itself; third, components at the lowest level of a technology all harness some natural phenomena. Besides these three aspects, technologies are “purposed systems,” meaning that they address certain real-world problems. To put it simply, technologies act as bridges that link real-world problems with natural phenomena. The nature of this bridge is recursive, with many components intertwined and stacked on top of each other.

On one side of the bridge, it’s nature. And that’s the domain of natural science. On the other side of the bridge, I’d think it’s social science. After all, real-world problems are all human centric (if no humans are around, the universe would have no problem at all). We engineers tend to oversimplify real-world problems as purely technical ones, but in fact, a lot of them require changes or solutions from organizational, institutional, political, and/or economic levels. All of these are the subject matters in social science. Of course one may argue that, a bike being rusty is a real-world problem, but lubricating the bike with WD-40 doesn’t really require much social changes. But I’d like to constrain this post to big real-world problems, and technologies that have big impact. After all, impact is what most academics seek, right?

Applied science is rooted in natural science, but overlooks in the direction of real-world problems. If it vaguely senses an opportunity for application, the field will push to find the connection.

Following this train of thought, application science should fall somewhere else on that bridge. Is it in the middle of the bridge? Or does it have its foot in real-world problems?

Loose ends

To me, at least the field of robotics is somewhere in the middle of the bridge right now. In a conversation with a computational neuroscience professor, we discussed what it means to have a “breakthrough” in robotics. Our conclusion was that robotics mostly borrows technology breakthroughs, instead of having its own. Sensing and actuation breakthroughs mostly come from material science and physics; recent perception breakthroughs come from computer vision and machine learning. Perhaps a new theorem in control theory can be considered a robotics novelty, but lots of it initially came from disciplines such as chemical engineering. Even with the recent rapid adoption of RL in robotics, I would argue RL comes from deep learning. So it’s unclear if robotics can truly have its own breakthroughs.

But that is fine, because robotics solve real-world problems, right? At least that’s what most robotic researchers think. But I will give my 100% honesty here: when I write down the sentence “the proposed can be used in search and rescue missions” in my paper’s intro, I didn’t even pause to think about it. And guess how robotic researchers discuss real-world problems? We sit down for lunch and chitchat among ourselves why something would be a good solution, and that’s pretty much about it. We imagine to save lives in disasters, to free people from repetitive tasks, or to aid the aging population. But in reality, very few of us talk to the real firefighters battling wild fires in California, food packers working at a conveyor belts, or people in retirement homes.

So it seems that robotics as a field has somewhat lost touch with both ends of the bridge. We don’t have a close bond with nature, and our problems aren’t that real either.

So what on earth do we do?

We work right in the middle of the bridge. We consider swapping out some components of a technology to improve it. We consider alternatives to an existing technology. And we publish papers.

I think there is absolutely value in the things roboticists do. There has been so much advancements in robotics that have benefited the human kind in the past decade. Think robotics arms, quadcopters, and autonomous driving. Behind each one are the sweat of many robotics engineers and researchers.

But behind these successes are papers and works that go unnoticed entirely. In an Arxiv’ed paper titled Do top conferences contain well cited papers or junk? Compared to other top conferences, a huge number of papers from the flagship robotic conference ICRA goes uncited in a five-year span after initial publication [1]. While I do not agree lack of citation necessarily means a work is junk, I have indeed noticed an undisciplined approach to real-world problems in many robotics papers. Additionally, “cool” works can easily get published, just as my current advisor has jokingly said, “sadly, the best way to increase impact in robotics is through YouTube.”

Working in the middle of the bridge creates a big problem. If a work solely focuses on the technology, and loses touch with both ends of the bridge, then there are infinitely many possible ways to improve or replace an existing technology. To create impact, the goal of many researchers has become to optimize some sort of fugazzi.

“But we are working for the future”

A typical argument for NOT needing to be rooted in reality is that, research thinks about problems further in the future. I was initially sold but not anymore. I believe the more fundamental fields such as formal sciences and natural sciences may indeed focus on problems in longer terms, because some of their results are more generalizable. For application sciences like robotics, purposes are what define them, and most solutions are highly complex. In the case of robotics especially, most systems are fundamentally redundant, which goes against the doctrine that a good technology cannot have one more piece added or taken away (for cost concerns). The complex nature of robots reduces their generalizability compared to discoveries in natural sciences. Hence robotics may be inherently more “shortsighted” than some other fields.

In addition, the sheer complexity of real-world problems means technology will always require iteration and structural deepening to truly provide good solutions. In other words these problems themselves necessitate complex solutions in the first place. And given the fluidity of our social structures and needs, it’s hard to predict what future problems will arrive. Overall, the premise of “working for the future” may as well be a mirage for application science research.

Institution vs individual

But the funding for robotics research comes mostly from the Department of Defense (DoD), which dwarfs agencies like NSF. DoD certainly has real-world problems, or at least some tangible objectives in its mind right? How is throwing money at a fugazzi crowd gonna work?

It is gonna work because of probability. Agencies like DARPA and IARPA are dedicated to “high risk” and “high payoff” research projects, and that includes the research they provide funding for. Even if a large fraction of robotics research are “useless”, the few that made significant progress and real connections to the real-world problem will generate enough benefit to provide incentives to these agencies to keep the research going.

So where does this put us robotics researchers? Should 5 years of hard work simply be to hedge a wild bet?

The good news is that, if you have built solid fundamentals through your research, even a failed bet isn’t a loss. Personally I find my PhD the best time to learn to formulate problems, to connect the dots on a higher level, and to form the habit of continual learning. I believe these skills will transfer easily and benefit me for life.

But understanding the nature of my research and the role of institutions has made me decide to tweak my approach to the rest of my PhD.

What would I do differently?

I would actively foster an eye to identify real-world problems. I hope to shift my focus from the middle of the technology bridge towards the end of real-world problems. As I mentioned earlier, this end entails many different aspects of the society. So this means talking to people from different fields and industries to truly understand their problems.

While I don’t think this will give me an automatic research-problem match, I believe the continuous obsession with real-world problems will bestow on me a subconscious alertness to identify and understand the true nature of these problems. This may be a good chance to hedge my own bet on my years as a PhD student, and at least increase the chance for me to find areas where impact is due.

On a personal level, I also find this process extremely rewarding. When the problems become more tangible, it channels back more motivation and energy for me to do research. Perhaps application science research needs this humanity side, by anchoring itself socially and overlooking towards nature, across the bridge of technology.

A recent welcome speech by Dr. Ruzena Bajcsy, the founder of Penn GRASP Lab, inspired me a lot. She talked about the abundant resources at Penn, and encouraged the new students to talk to people from different schools, different departments, and to attend the meetings of different labs. Resonating with her philosophy, I reached out to her and we had a great conversation about some of the existing problems where automation could help. Finally, after a few email exchanges, she ended with four words “Good luck, think big.”

P.S. Very recently, my good friend and I did a podcast where I talked about my conversations with people in the industry, and potential opportunities for automation and robotics. You can find it here on Spotify.

References

[1] Davis, James. “Do top conferences contain well cited papers or junk?.” arXiv preprint arXiv:1911.09197 (2019).