This idea of “good science” has made its way through several academic circles I’m involved with: in large part because of the advent of AI integration with modern research labs, but also because funding has been significantly threatened in the past 2-4 years. More and more research labs are forced to choose the fast-track on their research, however that may seem, and I actively see a separation in the research community between the people readily embracing and leading AI-backed studies with the people scared to adopt AI for fear they’ll lose the human touch that had once made their research so valuable. Very few have correctly navigated the dichotomy, and I’m still trying to find balance as well.

This week, ICLR-2027 main paper conference submissions are due. I myself am submitting two papers, and am eagerly hopeful that they are positive contributions to the field of learning and interpreting representations. However, so far, ICLR-2027 has over 60k submissions, a completely unreasonable amount that cheapens the value of such a publication, prevents the venue from being pure towards its original goals, and places immense stress on reviewers.

In transparency, I am an “AI-power user”, and have recently upgraded to the Claude $200/mo plan to fund my more experimental research and parallelize my opportunities for discovery. However, I attempt to maintain a level of involvement that allows me to fulfill the principles of good science, which I aim to uncover over the course of this post. In this blog post, I hope to convey what my interpretation of “doing good science” is, in the style of a framework that is replicable and conducive to the success of the field. I believe we should not abandon the gifts that AI has provided to academia as an industry, of extreme task overlap and the speed to match the world of entrepreneurship and capitalism-driven movement (as I’ll get into). However, we must retain the qualities of good science that we’ve worked hard to build in the field, lest we risk self-collapse and the very implosion of science.

It is a profound and necessary truth that the deep things in science are not found because they are useful; they are found because it was possible to find them. — J. Robert Oppenheimer, American theoretical physicist

what is science?#

I define science as the act of furthering the accumulated knowledge of humanity, through systematic study of causation. The life cycle of science (greatly simplified) revolves around the following three steps: theory, hypothesis, evaluation.

I like to conceptualize the existence of knowledge as some physical irregular multi-dimensional polyhedron, of all the knowledge we observe. Science is the process of adding new material to this substrate. To provide a metaphor: when balancing misshapen rocks into a tower, we must respect the laws of physics and the foundation set by previous rocks. We also have the option, of adding rocks to stablize the existing structure’s magnitude in the 3 physical dimensions, or to add rocks that increase the structure’s magnitude. In science, we must build in ways that are productive on existing methods. Much of science corroborates the polyhedron, discovering different ways to ensure that it becomes more rigid (the first option). However, occasionally, we present claims backed by the existing foundation that push the polyhedron to be a greater magnitude. Very rarely, we tap into a new dimension entirely, in proposing certain KINDS of theories: the “jumps” of a field, which seem almost unfounded at the time they are proposed, and which change the shape of everything built after them.

To make these three kinds of science a little more concrete, I’ll pin each of them to a specific paper. A great example of stabilizing research is Deep Reinforcement Learning that Matters (Henderson et al., 2018), which showed that many reported results in deep reinforcement learning shifted drastically with something as small as the random seed or the codebase used, and proposed standards for reporting results so that future claims could actually be trusted. The paper didn’t make the polyhedron any larger, but it made much of what was already inside it far more rigid. For research of greater magnitude, I point to Deep Residual Learning for Image Recognition (He et al., 2016), which took the well-established convolutional neural network and added skip connections so that networks could be trained at depths of over 150 layers, winning the ImageNet competition in 2015 and becoming a building block of nearly every deep architecture since. It is a paper firmly rooted in the existing foundation, but it pushed that foundation much further than anyone had before. Finally, for research in a new dimension, the classic example is Einstein’s 1905 paper On the Electrodynamics of Moving Bodies, which introduced special relativity and redefined space and time themselves, two things nobody had considered in need of redefining. In AI, the closest example I can think of is Attention Is All You Need (Vaswani et al., 2017), which proposed throwing out recurrence entirely in favor of attention, a move that seemed almost unfounded at the time, and which went on to change the field forever.

Fundamentally, science progresses because of these latter two ideas. Research for the reinforcement of existing knowledge is great, but reinforcement can often come through a variety of venues, such as product development and and consumer adoption. By contrast, experimental proposals hinge on settings explicitly configured for science, to test ideas in environments that are primed to catch dangerousness and that focus on the discovery rather than the profit, eliminating as much bias and human desire from the result as possible.

science and ai#

Science used to take time, but with the rise of AI, the time it takes to go from an idea to a result has shrunk dramatically. Coding agents can implement an experiment in an afternoon, language models can summarize a literature review in minutes, and entire papers can now be drafted, run, and written up by pipelines that require little more than a prompt. ICLR-2027’s 60k submissions are only the most visible symptom of this. In my own research, I’ve been able to work on more projects at a time than I ever could before, maintaining the high-level theories behind each project and describing surgical implementations for AI to carry out.

However, I’d argue that speed was never the true bottleneck of science. Knowledge, as I’ve defined it, is theoretically infinite, and the time we have to discover it is finite, so doing good science is fundamentally a problem of resource allocation. The way I like to think about it is by personifying each idea as its own person: every research question is someone asking for our attention, and because our time is limited, we must inherently choose how to allocate it, which means that some ideas simply don’t get any love. Every time we pick a problem to work on, we are choosing who we let starve.

AI does change the math of this problem, but only partly. By accelerating the speed at which we can form hypotheses and evaluate them, AI gives us more attempts at the right problem, and so it increases the probability that we stumble onto something meaningful. But more attempts will never be worth as much as knowing where to aim, and it is this knowing that I refer to as taste.

I define taste as opinions motivated by experience, and skill as the ability to use experiences. Skill determines how well you can carry out an idea, while taste determines which ideas deserve to be carried out at all. This lines up with how others have described it: Chris Olah, in his 2021 note Research Taste Exercises, defines research taste as, roughly, the ability to choose good problems to work on, and Richard Hamming, in his famous 1986 talk You and Your Research, made a habit of asking scientists “What are the important problems of your field?” before asking them why they weren’t working on them. AI has become incredibly skilled, and it will only become more skilled over time. However, AI is unable to implement taste, because under my definition, taste is built from experience, and a model has no experience of its own to form opinions from.

Returning to the life cycle of science I laid out earlier, AI can always do the hypothesis and evaluation parts of science, and in many cases it already does them faster than we can. But taste is all about finding good theories, and it is the theory step that decides which questions get asked in the first place. If doing good science is a problem of resource allocation, then it is integral that we retain the theory step for ourselves, because we are the ones who choose the questions.

This is also why I don’t believe AI can achieve the “jumps” I described in the previous section. Stabilizing knowledge and even extending its magnitude are problems of building on top of the existing foundation, and AI is extremely good at building on top of what it has seen. A new dimension, however, is by definition not found within the existing foundation, and so it cannot be reached by an intelligence that only knows how to build from it.

what is “good science”?#

So, what is the value of science in the face of capitalism, or communism, or any other system that decides how a community allocates its resources? I’ll save most of my thoughts on these systems for a future blog post, but generally, I believe science diminishes under these systems because it is slow and inefficient when compared to profit. A product can be sold the moment it works, whereas a theory might take decades before anyone realizes it was right.

To me, science is about preserving the mechanisms by which we solve the resource allocation problem. It is our best estimation of the purest way to choose which problems need solving, because it chooses them through curiosity rather than profit, and through a fundamental understanding of the human experience that training a model is, at least right now, simply suboptimal at capturing. So, I define good science as science that protects this mechanism: science that uses taste to decide which ideas we feed and which we let starve, and that keeps the theory, and the choice of questions, in human hands.

where is science going? the sad ending#

It is no secret that AI will continue to accelerate the speed of discovery, and it’s certainly true that it will continue to encroach on more and more of our ideas. Soon, AI will accelerate discovery far beyond the speed of human understanding, and I have no doubt that many of us are going to larp understanding the things it discovers. As we become more removed from the process of science, we will lose our ability to have taste, to think deeply about a problem, to propose ideas of our own, and to be creative in the ways that science so desperately needs. Taste is built from experience, and if we stop experiencing the process of science ourselves, we stop building the very thing that lets us choose the questions.

The main worry I have with AI-accelerated research is that we stop controlling the directions we research in, resulting in the self-collapse I alluded to earlier. Going back to the division I drew in “what is science?”, AI-driven science will be incredibly good at reinforcing existing material, making the polyhedron more and more rigid at a speed we’ve never seen before. However, in handing over the process, we lose the mechanisms by which we get to propose research of a greater magnitude, or research in a new dimension entirely. We would be left with a structure that is perfectly stable and completely stagnant, and a science that only reinforces itself is a science that has stopped growing. It is this slow implosion, where the polyhedron stops expanding while we continue to celebrate how solid it is, that I fear most.

where is science going? the happy ending#

However, I don’t think this ending is inevitable. My thesis centers around two things: creating sustainable recipes for reproducing results and verifying experiments, as well as retaining human taste to continually prioritize the humanity aspect of science.

The first is the more practical of the two. A sustainable recipe means releasing the code behind a result, specifying the environment it was run in, and, now that so much of our research passes through AI, logging the prompts and agent traces that produced it, so that anyone can verify an experiment rather than simply trusting it. Additionally, if the goal is to further our knowledge base, all ventures into the field of science must be their own lego sets: complete with the pieces, a comprehensive set of instructions explaining how those pieces fit together, and written in a language that’s consistent with the other lego sets in the field, whether that be shared notation, common benchmarks, or open standards. This is why I believe so strongly in open-source research. A lego set that nobody else can open is only a trophy, but a lego set that anyone can take apart gives us the freedom and scaffolded inspiration to remix it with others and build something new.

The second is retaining taste, which I’ve spent most of this post on already. As AI takes over more and more of the hypothesis and evaluation, the theory must remain ours, because it is the theory that keeps science pointed towards the problems that matter to humans.

some things I’ve been practicing#

The following are the things I’ve been practicing, which together form the closest thing I have to a framework for doing good science. None of them are revolutionary, but each one is an attempt to protect the parts of research that are human.

• Blogging and journaling. I try to blog semi-consistently (as evidenced by this post), alongside more mindful journaling as a writing practice. Writing is where my opinions get formed, and if taste is opinions motivated by experience, then writing is how I make sure I actually have opinions of my own.
• Pen-and-paper annotation. When starting new work, I do a lot of my literature review by annotating papers by hand. It’s slower than asking a model to summarize them, but the slowness is the point, as it forces me to sit with each paper long enough to decide what I think of it.
• Time away from work. During the moments when I could be parallelizing AI (making breakfast, going on runs, mornings and evenings), I take the time simply to listen to silence and think. The brain’s default mode network, a set of regions that become more active when we’re at rest rather than focused on a task, has been linked to mind-wandering and to generating creative ideas, and I’ve found that a wandering mind is often where my best theories come from.
• Using AI like a scalpel rather than a hammer. One of my own quotes is “Use the scalpel, in a time when we are given a hammer for every screw.” I describe each use case surgically, in plain English, which has more or less become my coding language, and then verify that the instrument did exactly what I asked of it.

Fundamentally, all of these practices come back to the same thesis: we must give ourselves the space to be human!

q.e.d.#

Fundamentally, the arguments in this blog are rooted in a belief that a human’s goal is to elevate and preserve the human experience (I aim to talk about this in a future blog post, with the goal to describe my thoughts on capitalism and socialism).

People rarely get the chance to explain why they do what they do, and in research, they almost never do: papers explain what was found and how it was found, but rarely why the question was worth asking in the first place. However, I believe the why should be apparent through the work itself. In this way, the why is just another face of taste, since when someone has chosen their problem well, you shouldn’t need them to justify it, because you can see it in the work that they do.

A final note on “being human” - fundamentally, science is led by curiosity, desire, and selflessness. People work on hard problems because they can’t stop thinking about what the solution might be, and often-times, it is this curiosity that lets us make the jumps that push science into new dimensions. It is this curiosity which I hope we never let starve.

- Karthik