Self-Selection in Financial Literacy Education

We will conduct a lab-in-field experiment to study selection patterns in financial education. Participants are offered access to education material designed to improve their financial decision-making ability within the experiment. We study how demand (willingness to pay) for education varies with baseline ability and with the format and perceived difficulty of the education materials. To better understand the role of confidence in education investment decisions, we also elicit each participant’s perceived baseline ability and perceived benefits of education.

We investigate selection patterns in financial education and their implications for welfare. Using two complementary approaches, we examine how demand for financial education relates to the benefits that individuals receive. We pair rich administrative data with a lab-in-field experiment that incentivizes participation in financial education among individuals with low willingness to pay for such education. We measure demand for education, confidence (i.e., the participant's beliefs about their starting level of knowledge), and the perceived benefit of different types of education materials. To understand how the proliferation of new technologies, such as AI and online learning, can influence selection patterns, we vary the format and perceived cognitive difficulty of the education materials.

Participants first complete a baseline task in which they choose between different financial instruments. Then, we ask participants about their willingness to pay for three different types of education materials. The three types are a university lecture format, a short video format, and an interactive AI-powered learning assistant. We emphasize that all materials are based on the same content and vary only in presentation.

A subset of participants is then randomly assigned to complete one version of the education material. The education material is designed to teach participants the financial concepts needed to maximize their payment (bonus) in the experiment. Finally, participants complete a very similar set of endline tasks after either completing or not completing the education materials.

This experiment allows us to identify selection patterns, test for selection on treatment effects, and explore ways to change selection patterns. Our findings will shed light on how self-selection impacts the efficacy of financial literacy programs and inform efforts to target financial literacy education to those who benefit most.

2025-08-01

2026-10-01

We measure how demand for different types of education materials varies with an individual's starting level of financial knowledge. We measure an individual’s financial decision-making ability, demand for financial education (willingness to pay), and the treatment effect of education (or no education).

To measure financial knowledge, we design scenarios where there is a financial decision that maximizes a participant's monetary payout in the experiment. We then measure the mistake, or the difference between the participant's choices in the scenario and the choice that would have maximized their payout. We construct our measure of financial knowledge as a rescaled function of the mistake. We base our methodology on Ambuehl, Bernheim, and Lusardi (2022), which uses the difference between two equivalently valued complex and simply-framed financial instruments as the outcome. We collect both a baseline and an endline financial decision-making score. We also measure the change in the score, or the treatment effect under different education materials or under no education.

We use a multiple price list to measure demand (willingness to pay/willingness to accept) for different types of education. We exclude observations where individuals switch at multiple points in the multiple price list. We also conduct a version of our analysis using only the willingness to pay/willingness to accept elicitation for the first version of the education material as a robustness check.

We also measure confidence and perceived ability by asking participants to predict their performance on the baseline and endline financial decision-making questions. We count an estimated score as being correct if it is within a reasonable range (e.g. +/- 5 percentage points) of the actual score.

We measure confidence and perceived ability by asking participants to predict their performance on the baseline financial decision-making questions. We also ask participants to predict their performance on the endline questions for each version of the education materials and for no education material. We count an estimate as being correct if it is within a reasonable range (e.g., +/- 5 percentage points) of the actual score. We also measure overconfidence using the difference between the participant's actual ability and their perceived ability.

We will conduct an experiment where we offer participants different types of education material to identify selection patterns and measure treatment effects.

We offer participants different types of education material to study how demand varies with the perceived cognitive burden of the material. Versions of the education material include a university lecture version, a video version, and an AI version. We also measure the perceived cognitive difficulty of each version. We may also add additional versions of the education material in future iterations of the study or use a different question to measure financial decision-making ability if we are able to obtain additional funding. We will measure the treatment effect of each type of education material versus the control group, which receives no education material. We will also pool the treatment groups if the treatment effects are similar.

The treatment condition is assigned based on the willingness to pay elicitation for some participants, but is randomly assigned for the majority of participants. This allows us to measure how treatment effects vary with baseline ability and demand for education.

We plan to look at heterogeneity in starting ability, demand for education, and treatment effects by confidence, demographics (gender, race, income, experience with finance), views towards AI, and self-reported study experience. We also bin the results by confidence, ability, and the interaction between ability and confidence. We look at both the continuous measure of ability and the binned ability levels. For questions where there are common response patterns or biases (e.g., always choosing one allocation, always choosing one type of investment), we will also create groups by bias and examine the results by these groups.

Our participants will primarily be made up of college students at UC Berkeley or at other UC schools. We may also recruit participants who are not college students or recruit participants through online platforms such as Prolific if we cannot recruit enough UC Berkeley students. We may also exclude (or report results separately) students who have taken a personal finance class, UGBA 135, from the analysis since the survey asks about concepts taught in the class and about future interest in the class.

The treatment and control conditions will be randomly assigned by a computer. Treatment conditions will be assigned at the individual level. Within treatment status, the different versions of the education material will be randomly assigned at the individual level as well. The size of the treatment and control group will not be balanced in order to maximize power.

Treatment conditions will be randomly assigned at the individual level. A computer will choose a random subset of individuals to have one of their choices in the willingness to pay elicitation implemented. For the majority of participants, the treatment and control conditions will be randomly assigned. Within treatment status, the different versions of the education material will be randomly assigned at the individual level as well. The size of the treatment and control group will not be balanced in order to maximize power.

No

Treatment will not be clustered.

With our current funding we will target a minimum of 1,000 complete responses, however the final sample size will ultimately depend on the attrition rate. Complete responses are defined as surveys that have been fully completed with only coherent willingness to pay responses. Incoherent responses include participants who switch from willing-to-pay to unwilling-to-pay more than once on the multiple price list, or participants who switch from unwilling-to-pay back to willing-to-pay. Incoherent willingness to pay measures will be coded as missing and excluded from the analysis. Our ideal sample size is 1,200-1,600 responses, and we will target larger sample sizes if we are able to obtain additional funding. Treatment will not be clustered. Since we connect our experiment questions to a real personal finance class at UC Berkeley, we may decide to exclude responses from participants who have already taken the class if their responses look different from other participants. We will also exclude participants who provide incoherent willingness to pay responses. Based on pilots of the survey on Prolific, we expect the attrition rate from incoherent willingness to pay responses to be approximately 5-15%, however the exact attrition rate may be higher or lower for different participant groups.

We will target a minimum of 1,000 complete responses. The treatment-to-control ratio is 3:1, reflecting our design with three treatment arms and one control group. Our ideal sample size is 1,200-1,600 responses, but the final sample size will ultimately depend on the attrition rate and our ability to recruit enough participants to complete the survey. We may add additional versions of the education material in future versions of the study. We will target larger sample sizes if we are able to obtain additional funding. Treatment will not be clustered.

We use results from a pilot study on Prolific to calculate the minimum detectable effect size, assuming a Type I error rate of 5%, 80% power, a mean score of 50 (out of 100), and a standard deviation of 30. To be conservative, we use a slightly higher standard deviation than what was observed in the pilot study. The treatment-to-control ratio is 3:1, reflecting our design with three treatment arms and one control group. With a sample size of 800, the minimum detectable effect size is 10 percentage points (p.p.), meaning the treated group must improve by at least 10 p.p. more than the control group for the effect to be detectable. As the sample size increases, the minimum detectable effect decreases: with 1,000 observations, it drops to 9 p.p.; with 1,200 and 1,400 observations, it decreases further to 8 p.p.; and with 1,600 observations, it reaches 7 p.p. Due to funding constraints that limit our sample size, we do not expect to be adequately powered to detect differences in selection patterns across the different versions of the education material at conventional significance levels. Instead, we plan to examine the correlation between participants' willingness to pay for each treatment and their initial financial task scores, then test whether these correlations differ across treatments. Based on our power calculations, with a sample of 800 to 1,000 participants, we can only detect differences in correlations of approximately 15–20 percentage points or more–that is, the correlation between the baseline financial literacy score and the willingness to pay would need to differ by at least 15–20 percentage points across treatments to be statistically detectable. We believe such large differences are unlikely given the similar nature of the education materials.