Two Laws of Wanting, and One Misunderstanding of the Bitter Lesson

There are two laws of wanting that seem to contradict each other.

The first is that you get what you optimize for. If your goal is to publish one hundred papers, you can probably do it.

You will not merely become “more productive.” You will adapt to the reward function. You will split one idea into five papers, cherry-pick experiments, search over seeds and baselines until the table looks right, abandon questions that take too long, and learn exactly how much novelty is needed to survive review. If the system rewards papers rather than understanding, then producing understanding is optional.

Researchers are not exempt from reinforcement learning. Give people a sufficiently clear reward signal and enough optimization pressure, and they will hack it.

This scales to the research community. Once papers, citations, benchmark scores, or rankings become targets, the whole field starts optimizing against them. Most people do not need to be dishonest. The incentive structure is often easier to game than to openly bend. A hundred individually reasonable decisions can collectively produce a literature full of inflated novelty, selective evidence, and results nobody really believes will survive contact with reality.

The metric may have started as a proxy for scientific value. Optimization finds the distance between the proxy and the thing itself.

The second law says that the more you want something, the less likely you are to get it.

Suppose you want to write a paper that people will still read twenty years from now. There is no useful feedback signal for this goal. So you substitute things that currently look durable: a grand problem, a clean mathematical formulation, a universal theory, an elegant abstraction.

You are now optimizing for your present image of timelessness.

That is dangerous because important work often looks embarrassingly local when it first appears. It may solve one annoying engineering problem, explain one ugly empirical fact, or make one system finally work. Its generality becomes visible later.

Machine learning makes this especially obvious. A kernel method can look intellectually permanent because its assumptions are explicit and compressed into mathematics. A method trained on enormous amounts of internet data can look contingent on compute, hardware, optimization, and historical accidents.

But historical accidents are part of the world.

The internet exists. GPUs exist. Cheap distributed computation exists. Once those facts change, the useful inductive biases change with them.

A paper can remain beautiful after its method becomes obsolete. Another can look like a temporary engineering trick and end up redirecting an entire field.

This leads to a common misunderstanding of the bitter lesson.

People often read it as an argument for broader hypothesis classes and fewer inductive biases. That interpretation is too simple to be useful.

Choosing a learning algorithm always means choosing biases. Architecture, optimizer, initialization, normalization, and training dynamics all determine which solutions are reachable under finite compute. Two systems can represent similar functions and still behave completely differently in training.

There is no total ordering in which one architecture is simply “more general” or “more free” than another. RNNs and attention organize computation differently. In some formal settings, recurrence can represent computations that fixed-depth attention cannot easily express. That tells us surprisingly little about which one will dominate at scale.

The bitter lesson cannot choose an architecture for us.

There are countless architectures at roughly the same level of computational generality. Researchers try one family for years, learn how to initialize it, optimize it, scale it, and map it onto hardware. Eventually the architecture acquires an ecosystem.

Architecture research is an outer-loop optimization problem with extremely sparse rewards and extremely expensive evaluations.

This is why early failures mean so little. A new architecture may fail because the idea is bad. It may fail because the optimizer is wrong, the implementation is immature, the scale is too small, the hardware is hostile to it, or nobody has yet discovered the right training recipe.

A mature architecture arrives with years of accumulated hidden capital. The new architecture arrives alone.

So the comparison is rarely architecture against architecture. It is one immature idea against another idea plus ten years of engineering.

RNNs were pushed for years. Attention has now been pushed for years. In both cases, much of the progress came from people stubborn enough to keep exploring a computational structure long after the first few experiments had failed to settle the question.

Training a model gives dense feedback. Choosing how models should learn gives almost none.

We learned how to search over parameters with gradient descent. We still search over architectures mostly by running the research community itself as a slow, noisy, expensive optimizer. Its reward function is distorted by publication incentives, its memory is damaged by unpublished negative results, and its evaluations can take years.

This is the deeper version of the bitter lesson. Learning can absorb many decisions that humans once made explicitly. The prior moves upward.

The same thing happens with personal goals.

A concrete goal can be optimized aggressively. A distant goal such as scientific fame or intellectual immortality creates proxies almost immediately. Once the proxy appears, ambition starts hacking it.

Wanting one hundred papers may give you one hundred papers.

Wanting a timeless paper may give you a paper designed to look timeless.

The two laws are compatible. For goals that are close to action and under your control, strong intentionality is useful. For terminal outcomes that depend on history, other people, future technology, and luck, attachment should be weak.

Optimize hard where the feedback is real.

Be careful when the reward has to be invented.