paul graham coined the term "schlep blindness" to describe a specific cognitive bias in how people choose startup ideas. the idea is that your brain automatically filters out opportunities that involve tedious, unglamorous work before they even reach conscious consideration. an idea about a new social app or consumer product gets through the filter because it sounds fun and exciting. an idea about fixing payment processing doesn't get through because somewhere below the surface your brain has already registered "banks, regulations, technical tedium" and quietly dropped the idea before you could evaluate it. so you never seriously consider the payment processing problem even though — as the collisons proved — it's worth billions.
stripe is the canonical example precisely because it's so obvious in retrospect. every developer who tried to accept payments in the mid-2000s knows how bad it was — the obtuse APIs, the merchant account requirements, the multi-week approval process, the compliance overhead, the inconsistent documentation. it was genuinely terrible. and it was terrible for years, during which thousands of developers complained about it and essentially nobody built a proper solution. the collisons sat down and built the proper solution and became extremely wealthy. the opportunity was sitting there the whole time, clearly visible, just coated in schlep. the schlep is what made it an opportunity rather than a crowded market.
i think about this in contexts beyond startups. in research, the most impactful contributions are often tooling — software that makes other researchers more productive, datasets that didn't previously exist, infrastructure that enables new kinds of experiments. this work doesn't get cited the way theoretical results do. papers about better tooling don't win best paper awards. but a good tool deployed to a field can multiply the research output of everyone in that field, which is worth more in aggregate than many individual research contributions. the people doing it are competing against a much smaller pool than the people doing theory, because most researchers have unconsciously filtered out "build a tool" as insufficiently prestigious.
physics has a well-documented version of this: the traditional hierarchy that placed theorists above experimentalists, who were above engineers, who were above technicians. the value hierarchy didn't track actual impact. particle physics progressed because of the enormous machines built by the people lower in the status hierarchy. the theorists made predictions. the experimentalists built the machines that checked them. the machines cost billions of dollars and required extraordinary engineering. but the status hierarchy said theory was the important work, so the best people went into theory, and the field was gated on how fast it could attract and retain the people doing the less glamorous work.
the practical implication: when looking for problems to work on, pay particular attention to things that feel aversive in ways that aren't about the problem itself. if you're drawn to a problem area but keep finding yourself thinking "but that part involves dealing with X" (where X is banks, or regulators, or legacy systems, or manual data collection, or some other boring infrastructure), that feeling of aversion is a signal. it means the problem has a schlep component that filters out a lot of potential competitors. the value is often locked behind the thing everyone would rather not do.
one diagnostic: ask practitioners in a field what they spend time on that feels like a waste, or what tools they would pay for if they existed. not what features they want in their core product — what's the annoying auxiliary work that nobody has thought to automate or simplify. the answers are usually obvious after you hear them, and usually nobody has built solutions because the builders are drawn toward the exciting core problems and away from the tedious auxiliary ones. this is the opportunity.
the dangerous version of schlep blindness is recognizing it and still not acting on it. you identify the schlep, you understand it's an opportunity, you convince yourself that someone else will build it, and you go do something more interesting. someone eventually does build it. they win the market. the question "why didn't I do that" has a boring answer: you saw it and chose not to.