Do teams "choose to lose" to improve their draft position?
Like other sports leagues, the NBA awards the best draft picks to teams that perform the worst, in order to even out team quality over time.
Up until 1984, the worst teams in each of the two conferences flipped a coin for the number one pick. After that, draft choices went to teams in reverse order of their finish the previous season.
But because this system awarded better picks to worse teams, the NBA worried that this drafting method gave teams an incentive to lose. And so, for 1985, the league changed the rule so that the draft order became a lottery among all non-playoff teams. Once a team knew it was going to miss the playoffs, it would have no further incentive to lose – its draft position would wind up the same either way.
The new system, of course, didn't promote competitive balance as well as the previous one. Therefore, in 1990, the NBA changed the system once more. The draft order would still be determined by lottery, but the worst teams would get a higher probability of winning than the less-bad teams. There would still be some incentive to lose, the theory went, but much less than under the pre-1985 system.
(It's important to understand that the question isn't about whether players deliberately throw games. Teams can decide to increase their chance of losing in other ways -- sitting out stars, playing their bench more, giving good players more time to come back from injury, trying out a different style of defense, playing a little "safer" to avoid getting hurt, and so on.)
The repeated changes to the system provided a perfect natural experiment, and in a paper called "Losing to Win: Tournament Incentives in the National Basketball Association," economists Beck A. Taylor and Justin G. Trogdon check to see if bad teams actually did respond to these incentives – losing more when the losses benefited their draft position, and losing less when it didn't matter. (A subscription is required for the full paper – I was able to download it at my public library.)
The study ran a regression on all games in three different seasons, each representing a different set of incentives: 1983-84, 1984-85, and 1989-90. They (logistically) regressed the probability of winning on several variables: team winning percentage, opposition winning percentage, and dummy variables for home/away/neutral court, whether the team and opposition had clinched a playoff spot, and whether the team and opposition had been mathematically eliminated from the playoffs (as of that game). For the "eliminated" variables, they used different dummies for each of the three seasons. Comparing the different-year dummy coefficients would provide evidence of whether the teams did indeed respond to the incentives facing them.
One of the study's findings was that once teams were eliminated in 1983-84, when the incentive to lose was the strongest, they played worse than you would expect. That year, eliminated teams appeared to be .220 worse than expected from their W-L record.
That number is huge. Teams mathematically eliminated from the playoffs already have pretty bad records. Suppose they're .400 teams. By the results of this study, after they're eliminated, the authors have them becoming .180 teams! It seems to me, unscientifically, that if these teams – and that's the average team in this situation, not just one or two -- were actually playing .180 ball in a race to the bottom, everyone would have noticed.
The authors don't notice the .180 number explicitly, which is too bad – because if they had, they might also have noticed a flaw in their interpretation of the results.
The flaw is this: in choosing their "winning percentage" measure for their regression, Taylor and Trodgon didn't use the season winning percentage. Instead, they used the team's winning percentage up to that game of the season. For a team that started 1-0, the second entry in the regression data would have pegged them as a 1.000 team.
What that means is that the winning percentages used in the early games of the season are an unreliable measure of the quality of the team. For the late games, the winning percentages will be much more reliable.
For games late in the season, there will be a much higher correlation of winning percentage with victory. And games where a team has been eliminated are all late in the season. Therefore, the "eliminated" variable isn't actually measuring elimination – it's measuring a combination of elimination and late-season games. The way the authors set up the study, there's actually no way to isolate the actual effects of being eliminated.
For instance: the regression treates a 1-2 team the same as a 25-50 team – both are .333. But the 1-2 team is much more likely to win its next game than the 25-50 team. The study sees this as the "not yet eliminated team" playing better than the "already eliminated" team, and assumes it's because the 25-50 team is shirking.
The same pattern holds for the "clinch" variable. Teams that have clinched are .550 teams who are really .550 teams. Those are better than .550 teams of the 11-9 variety, and that's why teams that have clinched appear to be .023 points better than expected.
The same is true for the "opposition clinched" dummy variable (which comes in at .046 points), and the "opposition eliminated" variable (at .093 points).
All four of the indicator variables for "clinched" and "eliminated" are markers for "winning percentages are more reliable because of sample size." And it's clear from the text that the authors are unaware of this bias.
I'm not sure we can disentangle the two causes, but perhaps we can take a shot.
Suppose a .333 team is facing a .667 team. The first week of the season, the chance of the 1-2 team beating the 2-1 team is maybe .490. The last game of the season, the chance of the (likely to be) 27-54 team beating the (likely to be) 54-27 team is maybe .230. The middle of the season, maybe it's .350, which is what the regression would have found for a "base" value. (I'm guessing at all these numbers, of course.)
So even if eliminated and clinched teams played no differently than ever, the study would still find a difference of .120 just based on the late-season situation. The actual difference the study found was an "eliminated facing clinched" difference of .266 (.046 for "opposition clinched" plus .220 for "team eliminated"). Therefore, by our assumptions, the real effect is .266 minus .120. That's about .150 points – still a lot.
But that's a back-of-the-envelope calculation, and I may have done something wrong. I'd be much more comfortable just rerunning the study, but using full-season winning percentage instead of only-up-to-the-moment winning percentage.
Here are how the predicted marginal winning percentage changes for "eliminated" compare to the other seasons:
1983-84: -.220 (as discussed above)
and the changes for "opposition eliminated":
The middle year, 1984-85, is the year the authors expect the "eliminated" effect to be zero – because, once eliminated, there's no further way to improve your draft choice by losing. The results partially conform to expectations – the middle year shows a significantly lower effect than the other two.
The results for that middle year are not statistically significant, in the sense of being different from zero. The authors therefore treat it as zero – "nonplayoff teams were no more likely to lose than playoff-bound teams." I don't agree with that conclusion, as I complained here. However, the effect as seen is not that much different from our (probably unreliable) estimated size of the late-season effect. Subtract the two, and it might turn out that eliminated teams actually played no worse after being eliminated – just as the authors hypothesize. The standard errors of these middle-year estimates, though, are pretty high. As commenter Guy points out (in a comment to the post I linked to a couple of sentences ago), it would be better if the authors used more than one year's worth of data in studies like these. Although transcribing every NBA game for three seasons must have been a hell of a lot of work – is there a Retrohoop? – I agree that one season just isn't enough.
And, also, it's possible that 1984-85 unfolded in such a way to make the coefficients look different. If, that year, teams played the early part of the season entirely consistently with their eventual record, that would cause the "late-season" factor in the coefficients to be small. That is, if the standings after one week were exactly the same as the standings at season's end, the difference in reliability between late games and early games would be zero. That could account for all the apparent difference in the "eliminated" effect. It's unlikely, but possible – and I don't think there's any easy way to figure out a confidence interval for the effect without running a simulation.
As it stands, my personal feeling is that the authors have found a real effect, but I can't justify that feeling enough that anyone should take my word for it.
My bottom line is that the authors had a great idea, but they failed in their execution. Rerunning the study for more than one season per dummy, and using full-season winning percentages instead of just season-to-date, would probably give a solid answer to this important question.
(Hat tip to David Berri at The Sports Economist.)