Nov 11, 2026
9 min read
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The second piece in our series "A claim you have heard: did it hold up?", with the verdict rule written down before we read any result.
Glasp Research. Keisuke Watanabe, Glasp Inc.
Pay someone for something they already like doing, and they will do it less once the pay stops. Psychologists call this the overjustification or undermining effect.
Our question: in experiments, does a tangible reward (money, an award) for an interesting task lower how much people choose to do it once the reward is gone, compared with people never rewarded?
We could not read either original: both are closed access. What follows comes from their abstracts, and from how a later review describes them.
Deci (1971), in the Journal of Personality and Social Psychology, reports two laboratory experiments and one field experiment. People did an activity in three periods, the rewarded group being rewarded in the second only; the test was the change in motivation from the first period to the third, against an unrewarded group. The abstract says that with money "intrinsic motivation tended to decrease", and with verbal reinforcement and positive feedback it "tended to increase". It gives no sample sizes or test results. A 1999 review by Deci and colleagues describes the paid condition as $1 for each of four puzzles solved in a set time.
Lepper, Greene and Nisbett (1973), in the same journal, studied children who already showed interest in an activity. Some agreed to do it for an award, some got an award as a surprise, some got none. The abstract says the children who expected the award later showed "less subsequent intrinsic interest" than either other group. It gives no numbers.
We found one study that calls itself a direct replication of Deci (1971): Peters, Grauerholz-Fisher, Vollmer and Van Arsdale (2022). We read only its abstract. It reports 24 undergraduates doing puzzles through a baseline, a paid phase and a return to baseline: "both groups showed a decrease in engagement across the study, and individual data varied greatly", which gave no support for the effect. The abstract mentions no preregistration and has no effect size, so by our rule it cannot settle the question.
We found no preregistered or multi-site replication.
The dispute was fought with meta-analyses, which pool many experiments. We read one in full: Deci, Koestner and Ryan (1999), in Psychological Bulletin. It pooled 128 experiments run in the laboratory or under laboratory-like conditions, from 1971 to 1997, all with an unrewarded control group, all on tasks rated at least neutral in interest, with motivation measured after the reward had stopped.
Its central number: in 92 studies, people who expected a tangible reward later spent less free time on the task than unrewarded people, d = -0.36, with a 95% confidence interval of -0.42 to -0.30 (d is a standardised difference; minus means the rewarded group did less). The 92 results varied far more than chance would explain, so this interval is likely too narrow. Across all tangible rewards the drop was larger for children (d = -0.39, 57 studies) than for college students (d = -0.27, 38 studies), and for children given expected tangible rewards it was still there more than a week later, typically within two weeks (d = -0.53, 12 studies).
The same paper shows where the effect is missing. A reward given as a surprise after the task made no clear difference (d = 0.01, interval -0.20 to 0.22, 9 studies), and neither did a reward for simply taking part (d = -0.14, interval -0.39 to 0.11, 7 studies). On a dull task, rewards did not lower later free choice (d = 0.18, against -0.68 for the interesting task in the same 11 studies). What people said about their interest moved much less than what they did: d = -0.07 for expected tangible rewards. Praise raised free choice for college students (d = 0.43) but not clearly for children (d = 0.11, interval -0.11 to 0.34).
Rewards tied to how well people did are where the camps split. The 1999 paper finds a drop overall (d = -0.28, 32 studies): much larger when rewards shrank with poorer performance and the comparison group got no feedback (d = -0.88, 6 studies), still a drop against a group given the same praise (d = -0.20, 10 studies), and no clear effect against a group given the same bad news (d = -0.03, 3 studies), which the authors tentatively read as the bad news itself doing the damage. On self-reported interest, performance-linked rewards showed no effect (d = -0.01). Cameron, Banko and Pierce (2001), the critics, say in their abstract that when rewards are linked to level of performance, motivation measures "increase or do not differ". We could not read their full text, so we cannot compare their numbers.
The two sides agree that expected tangible rewards loosely tied to performance lower later interest in an interesting task. The critics' abstract says so ("Negative effects are found on high-interest tasks when the rewards are tangible, expected (offered beforehand), and loosely tied to level of performance"), while also concluding that "in general, rewards are not harmful to motivation to perform a task". Two earlier analyses by the critics, largely on the same studies, also found significant drops in free choice, as the 1999 paper reports them (d = -0.21 for all tangible rewards, -0.25 for expected ones). As far as the abstracts we read show, the quarrel is mostly over which rewards and how much it matters; a later re-analysis, below, questions whether either side's numbers can be trusted.
A 2001 article by Deci and colleagues in Review of Educational Research restates the same 1999 data for teachers; it adds no new studies.
Then the bias question. The 1999 paper's only check for missing studies compared published studies with unpublished dissertations and found no difference. In 2017, List, Kepes and McDaniel re-analysed both the 1999 data and the critics' 2001 data with standard publication-bias methods. In a six-page conference paper they report that none of the 1999 results was robust, that 98% of the 40 estimates they checked could be off by more than 40%, and that publication bias played a part in every one. They do not publish corrected numbers. They say the direction of the publication-bias effect "cannot be conclusively determined", but that outliers generally inflated the estimates, and they conclude that neither meta-analysis is trustworthy and that the theory behind the effect "has, based on our analyses, no trustworthy support". A 2023 doctoral thesis at the University of Turku is described in search results as correcting for publication bias; its repository refused our requests, so we could not check this and use none of its numbers.
Our rule, fixed in advance, takes the largest meta-analysis we could read in full and asks whether its interval for the claim's own case excludes zero. It does (-0.42 to -0.30). The rule then looks for conditions inside the claim: a kind of tangible reward with no clear effect (we found two, surprise rewards and rewards for taking part), an age group with no clear effect (none), and a much weaker effect on what people say (found). So the verdict is holds under stated conditions.
The conditions: the reward is expected, it is tied to doing the task, the task is rated at least neutral in interest, the setting is the lab, and the claim is about what people do, not what they say. And the size is in doubt: the 1999 numbers are not corrected for publication bias, and the one re-analysis we read says they could be off by more than 40%, publishes no corrected value, and cannot say which way publication bias pushed them, though it says outliers inflated them. Our rule changes a verdict only on a published corrected interval that includes zero. A re-analysis that calls the estimates untrustworthy without publishing one is a case our rule did not foresee; we report it here rather than let it move the verdict, and a reader may weigh it more heavily than our rule does.
Our first pass, on 11 November, reached "unclear", because we could read no meta-analysis in full. When the full texts became available the next day we applied the same rule again, unchanged.
It does not give a firm size. -0.36 is the uncorrected pooled figure.
It does not say that "people enjoy it less". Self-reported interest fell by about a fifth as much as free-choice behaviour.
It does not cover praise, surprise rewards, rewards for just taking part, or dull tasks.
It does not reach offices or classrooms. The 1999 analysis kept only laboratory-style experiments and left out field studies; delayed tests exist only for children. A 2014 meta-analysis on incentives and performance (Cerasoli, Nicklin and Ford, 183 studies) asks a different question, how well people perform while incentives are in place, and should not be read for or against this claim.
We wrote the protocol and verdict rule into a file before opening any source, but after reading an earlier screening note of our own that had reached a provisional verdict, so the rule was not written blind. Every figure here was re-read against its source on 12 November.
Deci (1971):
https://doi.org/10.1037/h0030644
Lepper, Greene and Nisbett (1973):
https://doi.org/10.1037/h0035519
Peters, Grauerholz-Fisher, Vollmer and Van Arsdale (2022):
https://doi.org/10.1037/bar0000245
Deci, Koestner and Ryan (1999):
https://doi.org/10.1037/0033-2909.125.6.627
Deci, Koestner and Ryan (2001):
https://doi.org/10.3102/00346543071001001
Cameron, Banko and Pierce (2001), abstract:
https://pubmed.ncbi.nlm.nih.gov/22478353/
List, Kepes and McDaniel (2017):
https://doi.org/10.5465/AMBPP.2017.242
Cerasoli, Nicklin and Ford (2014), abstract:
https://pubmed.ncbi.nlm.nih.gov/24491020/
This article was researched and written by Claude (an AI model by Anthropic) in a Glasp research run. No Glasp user data was used. Checks: read in full were Deci, Koestner and Ryan (1999), Deci, Koestner and Ryan (2001) and List, Kepes and McDaniel (2017), the first two from scanned copies whose machine-read text has some errors, so their figures were checked in the running text and, where repeated, in the paper's summary figures; read only as abstract were Deci (1971), Lepper, Greene and Nisbett (1973), Peters et al. (2022), Cameron, Banko and Pierce (2001) and Cerasoli, Nicklin and Ford (2014); the two earlier analyses from the critics' side (Cameron and Pierce 1994, Eisenberger and Cameron 1996) are known only from the 1999 paper's description; the 2023 Turku thesis was not opened. A second pass by the same AI session checked every number in this text against the full texts or abstracts, which is not an independent review; on 12 November a separate AI session checked the 1999 figures against the page images, re-applied the verdict rule and reached the same verdict, and its corrections are included. No human has checked these figures.