Firefighting Drones

I believe that living truthfully has to include the parts of my work that did not go the way I hoped. This is a post about my time at The AirLab, under Prof. Sebastian Scherer, working on uncertainty and semantics-aware navigation for quadrotors in wildfire environments. It is also a post about realizing I had been treating research like something I could just dive into, and that this was a mistake.

I spent about a year on this. I did not leave with a paper, a deployed policy, or a result I would stand behind as finished. What I left with was a much more honest picture of myself as a researcher, and it was humbling.

The problem I wanted to work on

Wildfire is a genuinely hard robotics environment. The world is visually degraded, constantly changing, and full of objects that look similar while meaning very different things. Smoke is not a tree. A firefighter is not an obstacle in the same way a rock is. Geometry alone does not tell you what is safe to fly near, and a policy that cannot represent its own uncertainty is a dangerous thing to put in the air.

That is the work I wanted to be part of. The lab already had a wildland fire monitoring platform and a lot of people who understood the domain far better than I did. I showed up excited, and I treated excitement as a substitute for knowing how to run a research project.

Diving in

The first semester I tried to build a safety layer out of neural control barrier functions and Hamilton-Jacobi reachability, sitting on top of differentiable simulation. I thought if I could combine these tools I would get something that was both learnable and formally safer. I implemented enough of it to find out that the combined formulation did not provide a meaningful benefit, and that it was not feasible to keep pushing.

That was a negative result. I had understood, in the abstract, that negative results are part of research. I had not understood what it would feel like to spend months on something and then have the honest conclusion be that it did not work.

After that I pivoted toward uncertainty and semantics-aware reinforcement learning for reach-avoid tasks. I spent four days writing out a formulation from first principles. Those four days were some of the most fulfilling of my life in terms of work. I felt like I was finally doing research instead of following a recipe. Yikuan and Andrew were incredibly generous in helping me through ideas that were new to me, and I am still grateful for that.

Looking back, even that high was part of the same pattern. I wrote the formulation quickly because I was excited, not because I had earned a deep understanding of the problem. I built a lot around it. A perceptual oracle. An attention-based architecture. A scene generator. A belief reach-avoid environment with multiple semantic classes. A custom loss. A curriculum over uncertainty and semantic structure. I also started a small theoretical question I still think is interesting: when does semantic understanding actually help, even if the robot already has perfect geometric information?

I was moving. I was producing artifacts. I was not yet doing research carefully.

The thing I should have noticed sooner

In the second semester I kept going. I hit the milestones I had written down for myself. Then, while trying to finish the comparisons and the hardware story I had promised, I ran into a much more basic problem.

The project had grown larger than I could realistically execute. More importantly, the findings would only have been valid if the simulator itself was incredibly high fidelity. It was not. I had been building methods whose conclusions depended on a world model I could not actually trust. That is not a small implementation issue. That is the ground giving out under the work.

I should have seen this earlier. I didn’t, because I had been optimizing for making progress instead of asking whether the question was well posed.

Omar had suggested at some point that I look at expanding SALON into a drone setting. SALON is a self-supervised method the lab developed for off-road ground robots, where the system adapts its traversability estimates online from its own experience. I was interested in that, and in bringing uncertainty-awareness into it. I refactored the codebase into pure functions orchestrated through ROS2, spent a long time learning the foundational ideas I had skipped over (self-supervised learning among them), and finished formulating how the scheme could extend into 3D so a drone could operate with it.

That took longer than I expected, which should have been a signal. I was still catching up on the theory while trying to invent an extension of it. I did not get this to a place where I would call it a result.

What I actually learned

I used to think research was mostly about having an idea and then working very hard to implement it. That is how I had succeeded at a lot of other things. It is not how this works.

Halfway through the second semester I started to feel, viscerally, how much faster things go after you take the time to understand every little detail before you try something. I also learned that scope is not a managerial afterthought. If you do not decide what the project is, the project will decide for you, and it will decide to become too large and too unfocused to answer anything.

I need to learn how to do research. Not how to be busy in a lab. Not how to generate formulations and code. How to pick a question that can actually be answered, how to know what would count as evidence, how to notice when the experimental substrate cannot support the claim, and how to stop myself from diving in because diving in feels like progress.

This was a humbling year. I am trying to live more truthfully, and part of that is saying this in public instead of writing a project page that makes the work sound cleaner than it was. I failed at the version of this project I had imagined. I am not done becoming the kind of person who can do this well. I am just finally aware that I have to learn it.