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Field
Abstract
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Before
This study evaluates the persistence over time of the effects of two randomized information interventions—on longevity and on financial literacy—on individuals' survival expectations, economic/financial choices, and long-term-care (LTC) needs and perceptions. It is a second, longer-term endline of the randomized controlled trial registered as Dal Bianco et al. 2026, "Survival and Financial Literacy in Investment Decisions Later in Life," AEA RCT Registry, May 07, https://doi.org/10.1257/rct.18209-1.1 (Survey 1 hereafter).
We re-contact approximately 3,200 of the 3,600 UK residents aged 50–70 already interviewed in Survey 1, recruited via Prolific. Survey 1 was conducted in May 2026; data collection for the present wave is planned for July 2026, about two months after the intervention.
In Survey 1, participants were randomly assigned, at the individual level and with equal probability, in a 2 × 2 factorial design, to one of four groups receiving: (i) information on age- and gender-specific survival probabilities (survival-literacy, S), (ii) information on the returns and risks of financial investments (financial-literacy, F), (iii) both (S+F), or (iv) no information (control). The present wave administers no new intervention and performs no new randomization: identification rests entirely on this original random assignment. Because assignment was random, comparing treatment arms at this wave yields unbiased estimates of the causal effect of each treatment—separately and combined—on beliefs and behavior about two months after exposure; that is, the persistence of the treatment effects. Measuring the outcomes at a later date does not change the experimental nature of the comparison.
The study examines: (i) the persistence of the information treatments over time; (ii) financial behavior, stated intentions and market participation; (iii) demand for financial-literacy knowledge; (iv) the gap between subjective and objective survival probabilities; and (v) LTC needs and perceptions, including the subjective uncertainty around them.
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After
This study evaluates the persistence over time of the effects of two randomized information interventions—on longevity and on financial literacy—on individuals' survival expectations, economic/financial choices, and long-term-care (LTC) needs and perceptions. It is a second, longer-term endline of the randomized controlled trial registered as Dal Bianco et al. 2026, "Survival and Financial Literacy in Investment Decisions Later in Life," AEA RCT Registry, May 07, https://doi.org/10.1257/rct.18209-1.1 (Survey 1 hereafter).
We re-contact approximately 3,400 of the 3,600 UK residents aged 50–70 already interviewed in Survey 1, recruited via Prolific. Survey 1 was conducted in May 2026; data collection for the present wave is planned for July 2026, about two months after the intervention.
In Survey 1, participants were randomly assigned, at the individual level and with equal probability, in a 2 × 2 factorial design, to one of four groups receiving: (i) information on age- and gender-specific survival probabilities (survival-literacy, S), (ii) information on the returns and risks of financial investments (financial-literacy, F), (iii) both (S+F), or (iv) no information (control). The present wave administers no new intervention and performs no new randomization: identification rests entirely on this original random assignment. Because assignment was random, comparing treatment arms at this wave yields unbiased estimates of the causal effect of each treatment—separately and combined—on beliefs and behavior about two months after exposure; that is, the persistence of the treatment effects. Measuring the outcomes at a later date does not change the experimental nature of the comparison.
The study examines: (i) the persistence of the information treatments over time; (ii) financial behavior, stated intentions and market participation; (iii) demand for financial-literacy knowledge; (iv) the gap between subjective and objective survival probabilities; and (v) LTC needs and perceptions, including the subjective uncertainty around them.
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Last Published
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Before
July 13, 2026 07:17 AM
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After
July 13, 2026 07:44 AM
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Planned Number of Observations
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Before
Approximately 3,200 individuals (subject to re-contact response).
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After
Approximately 3,400 individuals (subject to re-contact response).
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Sample size (or number of clusters) by treatment arms
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Before
Approximately 800 individuals in each of the four groups selected among Survey 1 respondents: control, survival literacy treatment only, financial literacy treatment only, and combined treatments.
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After
Approximately 850 individuals in each of the four groups selected among Survey 1 respondents: control, survival literacy treatment only, financial literacy treatment only, and combined treatments.
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Field
Power calculation: Minimum Detectable Effect Size for Main Outcomes
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Before
Power assumes two-sided tests, α = 0.05, power = 0.80, individual-level randomization (no clustering). Main treatment effects pool two arms vs. two arms, giving approximately 1,280 vs. 1,280 at the planned analytic sample (640/arm assuming a retation rate of 80%).
Survival (primary 1). Immediately after the video, the survival treatment moved the raw gap by about 2 percentage points. Comparing arm means alone, we could detect persistence only if roughly 87% of that effect survived (MDE approximately 1.7 pp) — i.e., only a barely-attenuated effect. Adjusting for the pre-treatment population belief, a covariate that strongly predicts the outcome, removes enough noise to bring the threshold down to about 1.4 pp (planning scenario), so we remain powered even if the effect has faded to roughly two-thirds to three-quarters of its original size.
A more optimistic covariate assumption or the 800/arm ceiling lowers the MDE slightly further; the control-arm SD as a conservative input raises it to about 1.5 pp — none of which changes the conclusion. The same logic applies to the population-survival gap, where the pre-treatment baseline is of the same construct and if anything stronger. The MDE refers to the pooled main effect; a single-arm contrast (e.g., survival vs. control alone) is powered only for the full 2 pp effect.
Financial-literacy knowledge (primary 2). The outcome is the share of correct answers on the four comprehension vignettes. Because these items are new to the follow-up, there is no same-construct Survey 1 baseline to adjust for, so — unlike the survival outcome — no covariate reduction is applied (a deliberate, stated asymmetry between the two primary outcomes). Using a provisional standard deviation of 0.30, the design detects a main effect of about 3.3 percentage points in the share correct. This value is provisional; the items were written to be harder than the post-treatment attention checks (which approximately 93% of treated respondents passed) to avoid a ceiling effect that would erode power, and the standard deviation will be updated from the pilot.
Most-biased subgroup (best-powered persistence test). The immediate effect is highly concentrated: among the third of respondents with the most downward-biased pre-treatment population belief (bottom tertile of that variable), the Survey 1 effect is 7.56 pp — nearly four times the full-sample average — with a within-arm SD of approximately 17. Restricting to this tertile cuts sample size by roughly three (213 per arm at 80% retention, 426 vs. 426 in the main-effect contrast), which raises the MDE to about 3.3 pp. Because the effect grows far more than the MDE, this is the study’s most detectable persistence test: it remains significant even if only about 44% of the immediate effect survives, versus about 70% for the full-sample primary. This makes it the analysis most tolerant to the two-month attenuation we are most concerned about, and we pre-specify it accordingly. Two points are noted: the subgroup is defined on a pre-treatment variable, so randomization holds within it and the contrast is an unbiased causal effect; and re-contact must be tracked within the tertile, since the most mis-calibrated respondents may also attrit differentially.
Interaction effects in the 2 × 2 design require far larger samples and are exploratory.
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After
Power assumes two-sided tests, α = 0.05, power = 0.80, individual-level randomization (no clustering). Main treatment effects pool two arms vs. two arms, giving approximately 1,360 vs. 1,360 at the planned analytic sample (640/arm assuming a retation rate of 80%).
Survival (primary 1). Immediately after the video, the survival treatment moved the raw gap by about 2 percentage points. Comparing arm means alone, we could detect persistence only if roughly 87% of that effect survived (MDE approximately 1.7 pp) — i.e., only a barely-attenuated effect. Adjusting for the pre-treatment population belief, a covariate that strongly predicts the outcome, removes enough noise to bring the threshold down to about 1.4 pp (planning scenario), so we remain powered even if the effect has faded to roughly two-thirds to three-quarters of its original size.
A more optimistic covariate assumption or the 800/arm ceiling lowers the MDE slightly further; the control-arm SD as a conservative input raises it to about 1.5 pp — none of which changes the conclusion. The same logic applies to the population-survival gap, where the pre-treatment baseline is of the same construct and if anything stronger. The MDE refers to the pooled main effect; a single-arm contrast (e.g., survival vs. control alone) is powered only for the full 2 pp effect.
Financial-literacy knowledge (primary 2). The outcome is the share of correct answers on the four comprehension vignettes. Because these items are new to the follow-up, there is no same-construct Survey 1 baseline to adjust for, so — unlike the survival outcome — no covariate reduction is applied (a deliberate, stated asymmetry between the two primary outcomes). Using a provisional standard deviation of 0.30, the design detects a main effect of about 3.2 percentage points in the share correct. This value is provisional; the items were written to be harder than the post-treatment attention checks (which approximately 93% of treated respondents passed) to avoid a ceiling effect that would erode power, and the standard deviation will be updated from the pilot.
Most-biased subgroup (best-powered persistence test). The immediate effect is highly concentrated: among the third of respondents with the most downward-biased pre-treatment population belief (bottom tertile of that variable), the Survey 1 effect is 7.56 pp — nearly four times the full-sample average — with a within-arm SD of approximately 17. Restricting to this tertile cuts sample size by roughly three (227 per arm at 80% retention, 454 vs. 454 in the main-effect contrast), which raises the MDE to about 3.2 pp. Because the effect grows far more than the MDE, this is the study’s most detectable persistence test: it remains significant even if only about 42% of the immediate effect survives, versus about 70% for the full-sample primary. This makes it the analysis most tolerant to the two-month attenuation we are most concerned about, and we pre-specify it accordingly. Two points are noted: the subgroup is defined on a pre-treatment variable, so randomization holds within it and the contrast is an unbiased causal effect; and re-contact must be tracked within the tertile, since the most mis-calibrated respondents may also attrit differentially.
Interaction effects in the 2 × 2 design require far larger samples and are exploratory.
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