Commitment and consistency

The canonical demonstration is smaller and stranger than its reputation. Freedman and Fraser (1966) telephoned households twice, three days apart; the second call was identical for everyone, asking to send five or six men into the home for two hours to go through the cupboards and classify every household product. Compliance was 52.8% from people who had already answered eight questions about household soaps, 33.3% from those who agreed to answer and were then told they might be contacted, 27.8% from those who heard the questions but were never asked them, and 22.2% from those who received only the large request. Only the condition where the small request was actually performed beat the control; agreeing without doing differed from neither. Their second experiment is the famous one: 76.0% accepted a large, poorly lettered “Drive Carefully” sign for the front lawn after a small request on the same issue, against 16.7% of controls. The detail usually dropped is that the condition whose first request shared nothing with the second — different issue, different task, different person, weeks apart — still produced 47.4%, which is hard to read as consistency with a prior position and easy to read as a self-image as the kind of person who helps.

The meta-analytic record is modest. Beaman, Cole, Preston, Klentz and Steblay (1983) pooled 120 experimental groups and called the effect replicable but weak, with nearly half the studies producing no effect or an effect in the wrong direction. Burger's (1999) review puts the three earlier meta-analyses at r = .09 to .17, and his own pooled odds ratios locate where the effect lives: 1.47 when the first request was performed against a non-significant 1.16 when it was only agreed to, 1.91 when the second request continued the first task (53.28% compliance against 27.86% in controls), 1.58 when the first request demanded real involvement, and a weak 1.21 (r = .05) when the same person asked again with no delay — a cell in which about half of 24 studies favoured the control group, which Burger reads as reactance at a violated norm of give-and-take. Two manipulations reliably destroy it: telling people that few others comply, and paying them for the first step. Direct replication has not been kinder, either: Gamian-Wilk and Dolinski (2020) re-ran the original household-products procedure and found it worked in Ukraine but not Poland in 2003 and in neither country by 2013. The escalation form of this principle survives only where the user completes the first step themselves, unpaid, and the next ask continues the same task.

The version that reaches an interface is not request escalation but asking a question. Wood, Conner, Miles, Sandberg, Taylor, Godin and Sheeran (2016) meta-analysed 116 published tests of the question–behaviour effect, N = 54,985, and found d+ = 0.24, falling to 0.15 once funnel asymmetry was corrected for. The moderators matter more than the average: asking people to predict their behaviour gave d+ = 0.29, while asking only about intentions gave 0.12 with an interval containing zero. Effects were larger for socially desirable and easy behaviours, absent for risky ones (d+ = −0.05), larger in student samples than outside them (0.31 against 0.12), and shrank as the delay between question and behaviour grew. Rodrigues, French and Sniehotta (2016) contest even that, noting that Wood and colleagues included non-randomised studies and ran no risk-of-bias assessment: restricted to 33 randomised trials of health behaviour, their own estimate is d = 0.09 against Wood's 0.29 for the same domain, and two large preregistered trials — on colorectal cancer screening uptake and on organ donor registration — found no effect at all. Mechanism tests supported neither attitude accessibility, dissonance, behavioural simulation nor processing fluency, so an onboarding question is worth one screen at most, and has to earn the step it costs.

What holds up better is a commitment the user actively makes. Cioffi and Garner (1996) found that registering a volunteer decision by doing something produced more commitment than registering the identical decision by doing nothing, a difference that persisted over six weeks and showed up in behaviour — the empirical case for an explicit opt-in over a pre-ticked box. Baca-Motes, Brown, Gneezy, Keenan and Nelson (2013) had 2,416 hotel guests, unaware they were being observed, make a brief but specific commitment at check-in and wear a lapel pin for it: they were over 25% more likely to hang at least one towel for reuse, and hung over 40% more towels in total. Aggregated, this is real and small. Bergquist, Thiel, Goldberg and van der Linden (2023) pooled 10 meta-analyses covering 430 primary studies and put commitment approaches — goal setting, public commitments, implementation intentions — at d = 0.27 across 67 primary studies, behind social comparison (0.37) and financial incentives (0.32); publication-bias adjustment roughly halves that, to d = 0.14 under selection models and 0.13 under a weighted average of adequately powered studies. Plan for a few percentage points of behaviour, not a conversion lever.

The strongest-supported half of the principle is referencing the commitment later. Harkin, Webb, Chang, Prestwich, Conner, Kellar, Benn and Sheeran (2016) meta-analysed 138 randomised studies, N = 19,951, of prompts to monitor progress toward a goal and found d+ = 0.40 on goal attainment, with published and unpublished effects nearly identical (0.42 against 0.40). Monitoring whose results were physically recorded did better (0.43) than monitoring that was not (0.29), and private monitoring that was reported to someone did better (0.47) than private monitoring that was not (0.19). Public monitoring looked strongest at 0.55 but rests on three studies with an interval of [−0.16, 1.26], so “make it public” is the one piece of common advice here that the data does not carry. Locke and Latham (2002) give the shape of the thing being measured against: specific, difficult goals beat urging people to do their best, at .42 to .80, goal difficulty gives .52 to .82, and the relationship is strongest where the person is committed to the goal. A stored goal, a recorded count and a summary that puts one against the other is the best-evidenced screen in this entry.

One popular form has a clear null. Shu, Mazar, Gino, Ariely and Bazerman (2012) reported that moving a signature to the top of a form makes ethics salient and reduces dishonest self-reports; that paper has been retracted, and before the retraction Kristal, Whillans and colleagues (2020), working with the original authors, failed to replicate it across five conceptual replications (n = 4,559) and one highly powered preregistered direct replication (n = 1,235), observing no effect of signing first. In the same territory, Verschuere and colleagues (2018) pooled 19 direct replications of the moral-reminder experiment (n = 4,674) and found participants given a moral reminder reported solving 0.11 more matrices, 95% CI [−0.09, 0.31], Cohen's d = −0.04, against d = 0.48 in the original. A pledge box or a signature at the top of a form is not an honesty control.

The honest summary is mixed, and the grade depends on which claim you are buying. A voluntary, specific, actively made commitment that you record and reflect back is a defensible small intervention — d in the region of 0.13 to 0.27 once publication bias is accounted for. The escalation version, extract a small yes and then trade on it, rests on a 1966 study whose effect size has never been reproduced, a meta-analytic record where nearly half the studies found nothing or the opposite, and direct replications that came out null. The honesty-pledge version is retracted and replicated to zero.