Every MMA fan has an opinion about the USADA era. Fights got more cautious, or they didn’t. Fighters gassed less, or fans just remember the ones who did. I went looking for a rigorous, quantitative answer to whether independent drug testing actually changed how UFC fights play out, and found forum arguments and opinion pieces. Nobody had run the numbers.
So I ran them.
The setup
USADA started testing UFC fighters on 1 July 2015. That’s a real policy switch with a real date, which is the kind of thing you can actually test against, as long as you have something to compare the UFC to.
Bellator is that something. It’s the other major US MMA promotion, running the whole period without USADA testing of its own until PFL, which had already brought in USADA testing for its own roster in November 2023, bought Bellator about four months later. So for most of the window that matters, Bellator fighters were competing under the old rules the whole time UFC fighters were competing under the new ones.
That’s a difference-in-differences setup: watch the gap between the two promotions before July 2015, watch it after, and see whether the gap itself moved. Not “did the UFC change” in isolation (every combat sport has drifted over a decade) but “did the UFC change relative to a promotion that didn’t get the same policy.”
1,513 UFC fighters, 1,890 Bellator fighters, estimated with the Callaway-Sant’Anna staggered-adoption estimator.
The finding
Finish rate: fights ending by KO/TKO/submission rather than going to the judges.
The margin of error is more than double the estimate. This could easily be zero. The honest answer is: no detectable change.
Checking whether I could trust that
A null result is easy to get by accident: underpowered data, a bad comparison group, a method that just doesn’t pick up real effects. Before I believed my own “no effect,” I built two ways to try to break it.
Placebo dates. I reran the exact same comparison at 21 other dates, pretending the policy switch had happened then instead of July 2015. Seven didn’t produce a usable result and got dropped, leaving 14 fake dates to compare against. If July 2015 were special, it should stand out from that pile. It didn’t: the real estimate scored a p-value of 0.867 against the fake ones, meaning most of the made-up dates produced a result just as big as the real one. That’s what you want to see from a null. The actual date isn’t doing anything a random date wouldn’t.
Trying to fool my own method on purpose. This is the part I actually care about most, and it’s not the story I originally thought it was. Bellator’s data has a real seam in it, but not a slow one: PFL bought the promotion, and Bellator ran at most one more event under its own name before ceasing to exist as an independent promotion entirely. Include that last sliver of data in the comparison group, or cut it off right at the acquisition, and the estimate swings from the honest +2.2pp all the way to somewhere between -21.3pp and -25.5pp: a completely different, dramatic-looking, and wrong finding, produced by the exact same method with one careless specification choice.
That’s not composition bias in the usual sense. It’s not that Bellator’s fighters or judging quietly changed character over time. It’s that a promotion about to stop existing is not a stable thing to average into a trend line, and treating its last gasp as an ordinary data point manufactures a result that isn’t there. I built that failure mode on purpose and showed it, rather than noting “specification choices matter” as a footnote. If I can trick my own analysis that badly with one careless cutoff, so can anyone else’s, and a reader deserves to see it happen rather than take my word that I avoided it.
What this doesn’t cover
The fighters competing in each promotion changed a lot over this period, and not in matching ways: women’s fights grew into a much bigger share of UFC cards than of Bellator’s, and women’s fights finish less often. This specific estimate doesn’t correct for that yet, which means some of what looks like “no effect” could in principle be two composition shifts partly cancelling out rather than genuinely nothing happening. I’m flagging it rather than fixing it here because I’d rather be upfront about a limitation than quietly patch over it and imply the estimate is cleaner than it is.
The placebo test is also blunt with only 14 usable comparison dates, and it could easily miss a real effect that’s moderate in size rather than dramatic. And one of those fake dates happened to land on a real, unrelated anti-doping policy change made by a state athletic commission, which is exactly the kind of thing a placebo test is supposed to catch you assuming away.
Single promotion per treatment arm is also a real constraint on how much confidence the margin of error above should actually buy you. This is a rigorously null result on a narrow slice of a bigger question, not proof that USADA testing did nothing everywhere, for everyone, forever.
One line worth saying plainly: nothing here says or implies that any individual fighter, on either side of any comparison, used or did not use a banned substance. This is aggregate-level analysis about whether a policy shows up in fight outcomes, not a claim about anyone’s individual conduct.
Why I’m posting a null result
Because the null is the finding. A project whose predictions never fail, or whose results are always the exciting positive one, isn’t doing the checking. It’s finding what it went looking for. This one went looking for a real effect, built two separate ways to catch itself if the result was fake or fragile, and reported what came back.
Code, data pipeline, and the full placebo/specification-sensitivity checks are on GitHub. The live write-up with the full breakdown is here.