LifeSim Childhood: Extrapolating Intervention Effects and Public Cost Savings from Birth to Adolescence in the UK

The main data source used in LifeSim childhood is the Millennium Cohort Study (MCS), a longitudinal cohort study of around 19,000 children born in the UK around the year 2000. The MCS surveys were conducted when the children were 9 months, 3 years, 5 years, 7 years, 11 years, 14 years, and 17 years.⁴ After excluding twins and triplets and limiting our sample to those who responded to the age 3 survey, the final analytical sample consisted of 15,380 cohort members.⁵ The response rate for the MCS cohort declined over time, affecting the availability of outcomes measured at later ages. To deal with missing data we use multiple imputation using chained equations. We work with 30 sets of the multiply imputed data for the 15,380 children which we use for the regression analysis and simulation.⁶

The variables we use for our estimation from the MCS can be roughly divided into three categories: risk factors, confounders, and outcomes.⁷

The simulation in LifeSim Childhood runs a cohort of children picked from the MCS through the course of childhood several times or across several “universes” and produces the outcomes for each individual in the cohort in every universe. We perform a probabilistic sensitivity analysis using universes by introducing an element of randomness to the models built using the MCS.

We use the MCS data for the baseline characteristics of the cohort we run through the simulation. We use regression-based long-jump simulation which goes directly from the exposure to the outcome in each subsequent period without tracing out the mediating pathways at individual level (e.g. directly from age 3 to age 17). This is different from many other microsimulation methods such as the discrete event simulation approach we previously used in (Skarda et al., 2021) (the prior version of LifeSim) which use a “relay” approach, modelling outcomes sequentially period by period and tracing out the pathways at individual level. Both the long-jump and relay approaches to simulation have their benefits and downsides. The main difference is that the relay approach traces out full individual level causal pathways including mediating effects, whereas the long-jump approach only estimates total effects. The long-jump approach thus captures the total effect of all mediating pathways, without explicitly modelling those pathways, whereas the relay approach only captures the effects of mediating pathways that are explicitly modelled. The long-jump approach is potentially less conservative than the relay approach, for reasons explained later in the discussion section, but also more closely tied to the real long-term outcomes observed in the underpinning longitudinal data and potentially more comprehensive in the sense that it captures pathways that cannot be explicitly modelled using the relay approach.

We also prefer the long-jump modelling approach for LifeSim Childhood as a way to simplify the models to be estimated and minimise possible bias due to propagating bias and error from one period to the next. Since each effect is measured with some error/bias the error in the simulation when using the relay approach will likely increase with the number of years modelled. The long-jump simulation approach helps guard against this error being propagated and compounded through the model giving us estimates that are less likely to be biased.

In order to estimate the parameters for our long-jump modelling approach we run regressions estimating the effect of each risk factor on each outcome in each simulated year. We use linear regressions for cognitive ability (normal distribution), negative binomial regressions for SDQ scores and Kessler (count variables), and logistic regressions for the binary outcomes (Hospitalisation, disability, special education needs, truancy, exclusion, poor GCSEs, obesity, regular smoking, poor health). The point estimates as well as the variance of the estimates are extracted from the regression for use in the simulation. To get a nationally representative sample for estimation we use weights included in the MCS dataset, they adjust for attrition between the initial survey and the second sweep and the MCS’s sampling strategy.

The simulation is not deterministic, rather parameter uncertainty is captured in the model in the following two ways. First, the coefficients used to simulate the outcomes are randomly drawn from a normal distribution with a mean equal to the point estimate and standard deviation equal to the standard error from the estimates obtained. These coefficients are not restricted to being positive or negative and are randomly drawn from the full distribution. Second, an error term is added based on a random draw from the distribution of residuals to each estimate. Doing this allows us to capture some element of the variance of the outcomes. Additionally, in the case of binary outcomes, our estimates allow us to come up with a predicted probability of the outcome for each individual, we predict success for each individual by comparing the predicted probability with an individual random draw from a uniform distribution between 0 and 1.

In order to estimate the total effect magnitude in the absence of experimental or quasi-experimental data we follow Pearl (2009) in using directed acyclic graphs (DAGs) to specify the relevant causal pathways and guide choices about the selection of control variables. This allows us to bring together prior scientific knowledge to determine causal links between risk factors and outcomes in our data.¹⁶ The depth of information about the individuals and parents in the MCS allows us to capture a rich set of confounders in the relationship between our risk factors and outcomes using a set of model selection rules, so our models are credible, conservative, and parsimonious.¹⁷

The main limitation of MCS in terms of relevant confounders is the absence of genetic variables, biomarkers, and direct measures of some early childhood adverse experiences, such as abuse and neglect. Genetic and biomarker data would provide more direct information about inherited biological traits, while adverse early childhood experiences could potentially influence both parental income and later child outcomes. These are potential source of unobserved confounding, though some of these confounding effects will be indirectly captured through observed parental variables such as mother’s age at birth of the child, maternal smoking during pregnancy, highest parental education level, parental disability status, and parental lone parent status.

Furthermore, the causal status of many of these unobserved factors is not straightforward. Many inherited influences on later adverse outcomes are realised through cumulative developmental processes involving interactions between biological predispositions, early childhood experiences, and wider material and social environments, rather than through fixed impairments already determined at age 5 (Krieger, 2024; O’Donnell, 2024; Almond et al., 2018; Cunha and Heckman, 2007). Similarly, adverse experiences such as abuse and neglect may partly mediate the effects of low parental income on later outcomes, rather than acting only as pre-existing confounders. Our models include a rich set of observed parental characteristics, family circumstances, and early childhood conditions likely to capture part of these pathways. For comparison, we also estimate unadjusted associations and an “extra conservative” model using an expanded confounder set, including additional variables that may partly lie on the causal pathway. We discuss these issues further in the Discussion.

2.3.1 Model used for income as a risk factor

For our illustrative example, we run many different “long-jump” regressions to estimate the effect of early childhood income on many different childhood outcomes at many different ages, using the same basic model specification and control variables in each case. We run the simulation across three versions of our model, our preferred model that follows all the model selection rules, an “extra conservative” model that relaxes some of the rules, and unadjusted correlation. A simplified version of the DAG is presented in Figure 2.

Figure 2

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The confounders we include in the preferred model are indicators for country (England, Wales, Scotland and Northern Ireland, with England as baseline) at age 9 months, indicators for region within England (with London as baseline) at age 9 months,¹⁸ indicators for ethnicity of the child (with White as baseline),¹⁹ indicator for the mother’s smoking status during pregnancy, age of the mother at birth, indicators for highest education of parents at age 9 months (NVQ levels 1 to 5, with level 5 as baseline), indicator for any disability in the household at age 9 months,²⁰ and indicator for parent being the single parent at age 9 months (see Table A11).

In our extra conservative model we include an additional set of five confounders.

These include neighbourhood deprivation measured using the Index of Multiple Deprivation (IMD) fifth (with least deprived fifth as baseline) at age 9 months, poor maternal mental health (based on Rutter malaise score) at age 9 months, participation of at least one parent in the labour force at age 9 months, grandparents’ education reported at age 17 (NVQ levels 1 to 5, with level 5 as baseline), and disability of the child at age 3.²¹

IMD, maternal mental health, and disability of the child are not included in the main analysis as they may be mediators, i.e. they could all be affected by the parent’s permanent income and could affect the child’s outcomes.²² Additionally maternal mental health is also not included because it is measured at 9 months, and post-partum mental health may not be a perfect measure for mental health prior to birth/pregnancy. Parental labour force participation is not included as it is a major determining factor of income and its inclusion may not have a large effect on the child’s outcomes. Its inclusion could result in underestimating the effect of income. Finally, grandparent’s education is not included in the original model as it is used as a measure of wealth and is unlikely to have a large effect on the child’s outcomes except that through the parents’ education which we already account for.

The relationship between income and each of the outcomes we simulate is complex. Both risk factor and outcomes are affected by household composition, parental education, parental age, parental physical and mental health, parental wealth, parental socio-economic status, access to resources, child health, and genetics. The richness of data in the MCS about the child and the family allow us to control for many of the potential confounders in these relationships, either directly or indirectly (Wang et al., 2021). However, the MCS does not include information on all the potential confounders that may influence both parental income and childhood outcomes, such as genetic traits and early childhood adverse experiences, as discussed further in the Discussion.

The simulation estimates that at age 17, 38% of the population have poor GCSEs, 25% experience psychological distress, 26% are obese, 13% are regular smokers, and 10% have poor self reported health.²⁵ Figure 3 shows the percentage reduction in these adverse outcome across the entire population associated with each intervention. The error bars show the range in which 95% of the simulated sample effects lie.

Figure 3

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Scenario 1, increasing the income of the poorest fifth to that of the second poorest fifth results in a 4% (1.6 (0.44 - 2.66) percentage points) reduction in poor GCSEs, 0.4%(0.1 (-0.49 - 0.69) percentage points) reduction in psychological distress, 0.4% (0.1 (-1.10 - 1.31) percentage point) increase in obesity, 3.9% (0.5 (-0.65 - 1.63) percentage point) reduction in regular smoking, and 5.7% (0.6 (-0.3 - 1.44) percentage point) reduction in self reported poor health.

The other scenarios lead to reductions in all five adverse outcomes, including obesity, with larger reductions (percentage) in Poor GCSEs, self reported poor health, and regular smoking than in obesity or psychological distress.

Wellbeing in our case is measured by parent reported SDQ emotional symptoms scale linearly transformed to life satisfaction on a 0 to 10 scale. The simulated baseline levels of life satisfaction do not fluctuate significantly with age. Life-satisfaction peaks at age 5 with a mean of 7.9 and is lowest at age 17 with a mean of 7.14 (see Figure A3).

Figure 4 shows the average increase in life satisfaction for each scenario, to illustrate the size of the effects on life satisfaction we convert the results into WELLBYs. WELLBYs are defined as a one point increase in life satisfaction on a 10 point scale per child per year. In scenario 1, increasing the income of the poorest fifth to that of the second poorest fifth results in an increase in life satisfaction between 0.028 (-0.009 - 0.065, at age 5) and 0.043 (-0.003 - 0.090, at age 17) in a single year, for an annual average wellbeing increase (between ages 3 and 17) of 0.027 (0.016 - 0.038) or 0.404 (0.238 - 0.570) over the entire 15 year period.

Figure 4

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The other scenarios lead to greater improvements in wellbeing at every age resulting in a 15 year average wellbeing increase of 1.048 (0.796 - 1.299) in scenario 2, 1.312 (1.170 - 1.455) in scenario 3 and 3.214 (2.906 - 3.522) in scenario 4.

Our public cost estimates capture the costs associated with hospitalisation (ages 3 to 17), disability (ages 3 to 17), conduct disorder (ages 5 to 17), special education needs (ages 7 to 17),²⁶ persistent truancy (ages 11 to 17),²⁶ and permanent exclusion (ages 11 to 17).²⁶

The annual cost per child at the baseline increases with age as presented in Figure 5. The total annual cost per child is £396 at age 3, £604 at age 5, £1,795 at age 7, £2,296 at age 11, £2,345 at age 14, and £2,331 at age 17.²⁷ This averages to an annual cost per child between the ages of 3 and 17 years of £1,166.²⁸ This annual cost per child between 3 and 17 can be broken down into £187 for hospitalisation, £71 for disability, £128 for conduct disorder, £727 for special education needs, £3 for persistent truancy, and £50 for permanent exclusion.

Figure 5

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Figure 6 shows the cost savings associated with the implementation of each scenario. Note we do not account for the cost of achieving poverty reduction, rather we only show public cost savings. The figure shows four clustered bar graphs at each age, each bar is an estimate for scenarios 1 to 4 in order (from left to right). The area below the x-axis represents cost increases and the area above represents cost savings.

Figure 6

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Scenario 1 does not result in overall public cost savings (based on our six outcomes) at age 3 due to an increase in hospital costs compared to the baseline. The cohort average annual cost increases by £1.42 (-13.47 - 16.30) at age 3,²⁹ and results in savings of £7.60 (-8.15 - 23.35) at age 5, £10.35 (-96.72 - 105.96) at age 7, £79.48 (-59.67 - 158.93) at age 11, £29.87 (-69.90 - 126.32) at age 14, and £25.41 (-76.48 - 123.98) at age 17. This translates to an average annual cost saving between ages 3 and 17 of £18.75 (-15.04 - 41.95),²⁸ which can be broken down into an increase of £0.41 for hospitalisation, and savings of £0.67 for disability, £2.43 for conduct disorder, £10.19 for special education needs, £0.10 for persistent truancy, and £5.78 for permanent exclusion.

The cost savings in the other scenarios are statistically significant and increase (though there is still an increase in hospitalisation costs in scenario 2) as the money transferred increases. The cohort average annual savings between ages 3 and 17 years²⁸ are £96.81 (38.72 - 128.54) for scenario 2, £96.37 (67.47 - 126.82) for scenario 3, and £218.87 (115.10 - 322.64) for scenario 4.

While our results are primarily a demonstration of the tool, the increase in hospital utilisation with increase in income, though not significant, may be unexpected. From the literature, there is a plausible mechanism for increased inpatient hospitalisation due to an increase in parental income causing more proactive care seeking behaviour and earlier diagnosis of conditions, resulting in a general increase in non-emergency healthcare utilisation. However, there are very few studies (outside of the US and LMICs) looking at the effect of changes to family income on healthcare utilisation. Reinhold and Jürges (2012) find that healthcare utilisation among German children has an income gradient. Coughlan et al. (2022) find that children living in the most deprived parts of the UK were less likely to use primary and secondary health care but more likely to have emergency visits.

Table 1 summarises the effects of each scenario on a cohort of 700,000 (rough size of 2021 UK birth cohort) children over the full fifteen year period from age 3 to age 17

The first part of the table shows the number of children who avoid each adverse outcome under each simulated scenario as compared to the base-case model.

The next part of the table shows the public cost savings compared to the base-case model in millions of 2023 £s. There is a cost saving of 197 million £s with scenario 1 despite an increase in hospitalisation costs,²⁸ driven mostly by savings from reductions in special education needs and school exclusions. The costs savings are higher for the other scenarios.

The third part of the table shows the improvement in wellbeing in terms of WELLBYs, and the value of that increase with WELLBYs being valued at £13,000. For scenario 1 this results in £3,677 million worth of wellbeing generated over 15 years,³⁰ for a cohort of 700,000. ²⁸ The amount of wellbeing generated increases with the scale of the money transferred across scenarios.³¹

The final part of the table contains a rough estimate of the cost of the program, based on the minimum amount of money that would have to be transferred to each eligible household to move them to the target fifth of the income distribution. The amount of money that would have to be transferred to all household with newborns over the first five years in the poorest fifth to ensure they have at least as much as the lowest income in the second poorest fifth is £2,134 million.²⁸, ³²

The public cost savings (up to age 17) from each of the scenarios do not offset their costs. However, for scenario 1 this cost is more than offset by the value gained in terms of wellbeing, before taking into account the public costs savings and savings due to improvement in adverse outcomes and improved outcomes beyond age 17. However, the cost increases with each scenario with Scenario 2’s cost just about matching the sum of value generated in wellbeing and the public cost savings. For scenarios 3 and 4 the value of wellbeing generated dwarfs the costs (Table 1).

As a check of our model selection criteria and to get a sense of the effect of controlling for potentially missed confounders we compare our preferred model to an “extra conservative” model and an unadjusted model. Table 2 summarises the effects of each of the models in scenario 1 on a cohort of 700,000 (rough size of 2021 UK birth cohort) children over the full fifteen year period from age 3 to age 17.

The preferred model shows a reduction in all adverse outcomes except for obesity. In the extra conservative model, there is an increase in psychological distress and a larger increase in obesity than the preferred model, the improvements to the other adverse outcomes are more conservative as may be expected. The unadjusted model shows greater improvements than the preferred model in all adverse outcomes except psychological distress, where there is an increase in the number of cases.

The preferred model suggests with scenario 1 there is a cost savings of £197 million, compared to -£155 with the “extra conservative” model and £350 million, for the unadjusted model. This difference in cost is driven by increases in hospitalisation, disability and special education needs relative to the baseline in the extra conservative model coupled with lower savings on the other outcomes. The savings are higher across all six outcomes and positive across the board in the unadjusted model.²⁸

The preferred model shows greater wellbeing gains than the extra conservative model, both of which are much lower than the gains in the unadjusted model. Assuming the cost of implementing scenario 1 is £2,134 million as used above, the gain in value from wellbeing from any of the three models are greater than the cost.

Villadsen et al. (2023) look at the effects of scenarios 1, 2 and 4 on adverse outcomes using the MCS. However, they do not include any covariates in their base case estimation of the effects of these income shifting scenarios, and only include two covariates in sensitivity analysis. Consequently, the effects of each of the income shifting scenarios they report, after adjusting for just two covariates, are much larger than our more conservative estimates, roughly varying between 0% (obesity) and 6% (poor health) for scenario 1, between 2% (obesity) and 15% (poor health) for scenario 2, and between 13% (psychological distress) and 35% (poor health) for scenario 4. The general trend and ranking of effect sizes on the adverse outcomes however, is similar to ours.

We use a continuous measure of household income and report findings in terms of effect sizes so that we can compare our estimates with those from a recent systematic review (Cooper and Stewart, 2021). The review compares findings from different studies by reporting the effect of a $1000 (in year 2000 dollars) increase in income on effect sizes in terms of standard deviation changes for a wide range of outcomes including cognitive development, educational outcomes, child health, and social and behavioural scores. Using LifeSim we estimate the effect of a £676 (Year 2000 equivalent of $1000) increase in income on some of the human capital outcomes reported by Cooper and Stewart (2021) that have an analogue in the MCS. The effect estimates are the change in standard deviation of each outcome with an increase in income of £676. The estimates from Cooper and Stewart (2021) and LifeSim are reported in Table 3 and Table A10.

The estimates from LifeSim closely match those from Blau (1999), Votruba-Drzal (2006), Dearing et al. (2006), and Zachrisson and Dearing (2015). However, the estimates from Fernald et al. (2008), Dahl and Lochner (2012) and Gennetian and Miller (2002) who limit their study to poor households in Mexico, the US and Minnesota, respectively, are much larger than those in LifeSim Childhood. The effect sizes measured based on the equivalent sub-population in the simulation cohort. For example, results of a study focusing on poor households are compared to households in the bottom fifth of the income distribution. However, the estimates used in the simulation are still based on the full population and not specific sub groups. This may partially explain why estimates are more similar for the full population estimates in the systematic review. The estimates from Cooper and Stewart (2021) while broadly being similar to those from the MCS are not perfect for the purposes of our comparison as the interventions are different, they are not UK specific and are not all contemporary.

When comparing our MCS-derived estimates to external benchmarks from the existing literature, it is important to note both that we only compare positive outcomes and that published meta-analyses may disproportionately reflect positive outcomes. This can occur due to publication bias against null or negative results, or selective reporting within the reviews themselves, thereby potentially biasing these external benchmark estimates upward.

We estimate a long-term marginal effect of log household income in early childhood on life satisfaction at age 17 of 0.39 on a scale from 0 to 10 (Table A12). This implies that a permanent increase of 6.6% in log household income in early childhood - e.g. £1,000 pounds a year to a poor household at the 20th percentile of approximately £15,000 in 2023 - increases life satisfaction on average at age 17 by about 0.026 (6.6% * 0.39) of one WELLBY. This represents a population average effect of just over one quarter of one percentage point of the maximum life satisfaction score of 10.

Our estimate of 0.39 for the long-term effect of log childhood income on life satisfaction is similar in magnitude to the current best estimate of the long-term effect of log adulthood income on life satisfaction of about 0.38, according to two authoritative reviews of the literature by world leading experts on life satisfaction (Clark et al., 2019; Frijters and Krekel, 2021). The estimate of about 0.38 comes from a study by Lindqvist et al. (2020) of long-term outcomes for 3,362 large-prize lottery winners randomly selected from a large group of Swedish lottery players. This estimate is more generalisable to the general population than studies of small numbers of large-prize lottery winners randomly selected from a population of committed gamblers. This estimate of about 0.38 is also in line with estimates from analysis of observational data in 113 countries, which found that this estimate was remarkably robust across countries, within countries, and over time (Stevenson and Wolfers, 2008). Furthermore, one might expect that increased income during a sensitive period of childhood development would be more beneficial than increased income during adulthood. If anything, therefore, our estimate of 0.39 for the effect of log income in childhood is not only modest but might plausibly be considered an under-estimate.

In our illustrative example, we find that increased early childhood income substantially reduces adverse outcomes and improves wellbeing up to age 17. However, estimated public cost savings are relatively small compared with the monetary value of the wellbeing gains. For a cohort of 700,000 newborns, scenario 1 generates estimated public cost savings of £197 million up to age 17, discounted at 3.5%, compared with a gain of 282,840 WELLBYs. Valued at the standard UK Treasury value of £13,000 per WELLBY in 2019 prices, these wellbeing gains are worth £3,677 million. The monetary value of wellbeing gains is therefore about 20 times larger than the estimated public cost savings.

Assuming a hypothetical cost of £2,134 million over five years, scenario 1 results in an estimated net benefit of £1,740 million over 15 years for a single birth cohort. This benefit is almost entirely due to wellbeing gains rather than public cost savings. The cost per WELLBY is £7,545, below both the Treasury’s central value of £13,000 per WELLBY in 2019 prices and its lower bound value of £10,000. However, this should not be interpreted as an evaluation of a directly implementable policy. The scenario is a stylised illustration of the model and may understate the cost of real-world implementation, since it does not include administrative costs or deadweight losses and unrealistically assumes perfect targeting of additional income on families in the poorest fifth. On the other hand, the benefit side is also conservative in important respects, since we only include wellbeing gains for one child in the household, exclude potential effects on parents, siblings and other household members, and do not capture potential public costs savings from reduced numbers of children being taken into care and having other rare but costly adverse experiences that are not well captured in survey data.

The more ambitious income scenarios generate proportionately larger public cost savings and wellbeing gains. In our extra conservative model, with five additional controls variables that do not meet our model selection criteria, we still find substantial estimated total public cost savings and benefits to health, wellbeing and other life outcomes. However, we find slightly larger increases in hospitalisation costs, disability and special educational needs, though none of these estimates are statistically significant. These increases may reflect increased identification of need for these services, but our sample size and statistical power do not allow robust conclusions about the existence or magnitude of such effects.

Finally, we compare LifeSim Childhood estimates with estimates from the literature of the effects of a $1,000 increase in income on cognitive and socio-emotional scores in the US, Canada, Mexico and Norway. Our estimates are broadly consistent with this literature, particularly for full-population effects. Some studies focusing specifically on poorer groups find larger effects than those estimated using LifeSim Childhood.

LifeSim Childhood has several strengths. First, it allows researchers and policy analysts to estimate effect magnitudes for a range of early childhood risk factors across multiple outcomes up to age 17, including outcomes relevant to health, wellbeing, education and public costs. This is important because many early childhood policies have long-term and cross-sectoral consequences that are difficult to capture using conventional short-term evaluation methods.

Second, the model is based on the Millennium Cohort Study (MCS), a detailed, high-quality and nationally representative longitudinal dataset following more than 15,000 individuals born in the UK in 2000/01 from infancy to age 17. This allows LifeSim Childhood to model developmental pathways across the whole of childhood using repeated measures of family circumstances, child development and later outcomes.

Third, our estimation strategy uses observational data to estimate effect magnitudes for relationships that are already supported by external theory and evidence. The modelling strategy is based on pre-existing scientific understanding of relevant causal pathways, supported by a conservative approach to confounder selection and validation against estimates from a previously published systematic review.

Fourth, LifeSim Childhood uses simulation modelling to synthesise estimates from MCS with unit costs, wellbeing valuations and other external information (Table A2). This makes it possible to estimate long-term consequences for multiple outcomes and sectors, while also representing uncertainty. Finally, outputs from LifeSim Childhood can be linked to LifeSim Adulthood to simulate outcomes over the full life course.

The main limitation is that we do not use trial or quasi-experimental data to estimate the effect magnitude for each exposure-outcome pair. Comprehensive and consistent data of this kind, covering the full range of childhood risk factors and outcomes relevant to the UK context, are not available and are unlikely to become available in the foreseeable future. We therefore use observational data from MCS to parameterise our model, and our estimates are limited by the confounders available in that dataset.

LifeSim Childhood may overestimate effect magnitudes if important unobserved confounders are omitted. In practice, adjustment for additional confounding variables usually reduces estimated effects, and the unadjusted model produces larger estimated benefits across all outcomes. However, when we compare our estimated magnitudes with those from experimental and quasi-experimental studies, we do not find evidence of substantial overestimation. Insofar as omitted-variable bias is broadly similar across risk factors, this concern is also less problematic when LifeSim Childhood is used for relative comparisons of effect magnitude across different childhood risk factors, though this assumption may not always hold.

A specific limitation of MCS is the absence of genetic variables, biomarkers and direct measures of early childhood adverse experiences which are too rare or sensitive to be recorded accurately in survey data, such as death of a parent, bullying, violence, sexual abuse, or being a victim of a crime. Both inherited biological traits and exogenous early childhood adverse experiences could potentially influence both parental income and later childhood outcomes and hence act as unobserved confounders. However, the causal status of many of these potential confounding variables is not straightforward. Many inherited influences on later adverse outcomes are not expressed as fixed impairments already determined at age 5, but are realised through cumulative developmental processes involving interactions between biological predispositions and wider material and social environments. Similarly, many adverse experiences such as parental abuse and neglect may partly mediate the effects of low parental income on later outcomes, rather than acting only as pre-existing confounders.

Our models include a rich set of observed parental and family characteristics that may indirectly capture some of these unobserved pathways, including mother’s age at birth of the child, maternal smoking during pregnancy, highest parental education level, parental disability status, and parental lone parent status. For comparison, we also estimate unadjusted associations and an “extra conservative” model using an expanded confounder set which includes additional variables that do not meet our model selection criteria and may lead to under-estimation (e.g. maternal mental health, which may be a mediator that captures part of the total effect of parental income). We return to these issues below when considering the interpretation of LifeSim Childhood estimates.

A second limitation is that our public cost estimates are incomplete. They omit important rare but expensive outcomes, such as being taken into care and contact with the justice system. They also exclude some non-inpatient health care costs, costs associated with disability including social care and healthcare, and costs associated with school exclusion. LifeSim Childhood may therefore underestimate public cost savings.

Third, LifeSim Childhood focuses on outcomes for a single child, rather than for the entire household, and does not capture spillover effects on parents, siblings and classmates. This is important for household-level risk factors such as parental income, as our illustrative example does not capture the effects of parental income on the wellbeing of siblings or the parents themselves. It is also important for wellbeing analysis more generally, since impact on a child’s development and wellbeing may affect the wellbeing of other people.

A fourth limitation is potential cohort bias. We estimate effect magnitudes for Generation Z, born in 2000/01, but apply these estimates to Generation Alpha, born today. There is therefore a risk that relationships between early childhood risk factors and later outcomes have changed across cohorts due to generational changes in family life, public services, education, labour markets, health care, social norms and the wider policy environment.

Fifth, direct data on child-reported life satisfaction on a 0 to 10 scale were not available consistently from ages 3 to 17. We therefore use a proxy measure based on parent-reported SDQ Emotional Symptoms Score, which is measured consistently from ages 3 to 17. Sensitivity analyses using inconsistently measured child-reported subjective wellbeing measures at ages 11, 14 and 17 produce slightly lower WELLBY estimates (see Table A12), while analyses using parent-reported SDQ Internalising Score produce slightly higher estimates (see Table A7). Our central estimates were broadly consistent with external evidence on adult wellbeing effects (see also tables A6, A8 and A9).

Sixth, our probabilistic sensitivity analysis assumed that estimation errors around each causal parameter were all independent - i.e. zero covariance among the errors - since we do not have a methodology for estimating covariance structures among large numbers of separate estimates. In reality, however, covariance is unlikely to be zero: if one parameter is higher than our mean estimate then various other parameters are also likely to be higher. Our simplifying assumption may therefore tend to under-estimate overall uncertainty, insofar as independent errors may tend to cancel out more than correlated errors.

A further limitation is uncertainty about the relationship between exposure duration and long-term effect. For example, to obtain the estimated long-term effect of increased parental income in early childhood, the increase may need to last for one year, five years, ten years or longer. Similar issues arise for other exposures where the relevant duration is uncertain. This is a general challenge for extrapolating long-term intervention effects and is closely related to the problem of effect fadeout. In our illustrative income example, we sidestep this issue by not specifying the duration of change from one income quintile to another. In real-world applications, however, users would need to specify the intervention exposure duration and make assumptions about effect fadeout if the exposure is not permanent.

These findings should not be interpreted as showing that any specific income transfer would produce exactly the estimated effects, or that public cost savings alone are sufficient to justify early childhood income policies. Rather, the results illustrate how LifeSim Childhood can combine cohort evidence, theory-informed estimates of effect magnitudes, simulation modelling, unit costs and wellbeing valuation to estimate the potential long-term consequences of changes in early childhood risk factors.

The illustrative income example also highlights the importance of including wellbeing outcomes alongside public costs. In this application, the estimated economic case for increasing early childhood income depends primarily on wellbeing gains rather than fiscal savings to public services. This finding is important for policy appraisal, since interventions that improve children’s life chances may be undervalued if assessment focuses only on short-term service use or public expenditure.

Future work will address several of these limitations. First, we aim to improve and extend our unit cost estimates, including better modelling of the distribution of costs for each outcome and incorporation of rare but expensive outcomes such as being taken into care and contact with the justice system, using administrative data where possible.

Second, we plan to improve and validate our wellbeing measurement. This will include using other self-reported wellbeing measures available from age 11 onward, refining the mapping between childhood mental health and life satisfaction, and validating our current mapping using other UK datasets.

Third, we aim to assess the extent of cohort bias and update model parameters using the most recent estimates available from external data sources. This is important for applying estimates derived from children born in 2000/01 to children born today.

Fourth, our current models do not capture interactions between multiple risk factors or moderation of effects across population subgroups. Future work will explore the interrelationships between risk factors, beginning with moderation effects. This will allow LifeSim Childhood to provide more nuanced estimates for different population groups and intervention contexts.

LifeSim Childhood can help researchers and policy makers evaluate a wide range of early childhood interventions and policy scenarios. Users can map the short-term effects of an intervention onto one or more LifeSim Childhood risk factors, describe the relevant population of interest, and estimate long-term consequences for public spending, wellbeing and other life outcomes. Relevant applications could include not only income transfers but also early years services, parenting support, child nutrition programmes, school readiness interventions and child mental health support.

These methods are valuable because policy analysts often find it difficult to quantify the full long-term and cross-sectoral consequences of early childhood policies. LifeSim Childhood provides a transparent framework for estimating these consequences and for comparing the likely long-term impacts of different ways of investing in childhood. In doing so, it can help strengthen the economic case for early intervention while also clarifying whether the main expected benefits arise through public cost savings, improved wellbeing, better educational outcomes, or broader improvements in children’s life chances.

A non-exhaustive list of those consulted as part of our advisory group are included in appendix section A.9

These rules are described in detail with examples in appendix section A.6.

We assume our risk factor “permanent income ” affects outcomes from birth but we only model public costs and wellbeing gains from age three to age 17 in an effort to be conservative.

The study is ongoing and the next sweep of data from when the cohort members are around 23 was released in February 2026

3,705 children are dropped due to non response in the second sweep at age 3 and 396 children who are twins or triplets are dropped. Twin and triplet households are dropped entirely.

The imputation process is described in more detail in appendix section A.5

In this paper the three groups of variables will be mutually exclusive but this is not the case for LifeSim in general. Appendix section A.1 defines these terms in more detail.

Income fifths are based on the distribution of household income within the multiply-imputed MCS data with age 3 UK population weights.

The confounders are described in more detail in section 2.3.1 and appendix section A.2.2 (see also Table A3).

General Certificate of Secondary Education (GCSE) results in England, Wales, and Northern Ireland, and National 5 (N5) results in Scotland

or 4 or more N5 results in Scotland graded D or above

We provide more information about using this measure in appendix section A.4. We also present simulation estimates with SDQ internalising - the sum of emotional and peer problem scores - as the life satisfaction measure instead in Appendix Table A7.

Table A1 and A2 in the appendix summarise the details of the costs and their sources.

SDQ scores are also available at age 3 but we do not have a cost at that age and the algorithm we use to identify conduct disorder is not appropriately calibrated for this age group so we omit these outcomes.

The average cost per EHCP student is estimated at around £31,000 and the average cost for a non-EHCP student is estimated at around £5,500 in 2023.

Appendix section A.3 provides justification for assuming a causal relationship between early years income and our chosen outcomes

The rules along with examples of their application are presented in appendix section A.6

North East, North West, Yorkshire and the Humber, East Midlands, West Midlands, East of England, London, South East, and South West

White, mixed, Indian, Pakistani and Bangladeshi, Black or Black British, and other ethnic group (inc. Chinese and other Asian)

Measured by receipt of any disability benefits by either the main parent or partner.

This is excluded as a control when estimating the effect of income on disability.

Since mediators(M) lie on the causal pathway between the risk factor (RF) and outcome (O), their inclusion in the regression (assuming direction of the effect is the same in all three relationships, RF->O, RF->M, and M->O) will result in smaller estimates of the effect of the risk factor on the outcome.

They examined the effects of scenarios 1, 2 and 4 on the five adverse outcomes at age 17.

The distribution is presented in Appendix Figure A1.

The prevalence of these adverse outcomes in the MCS are slightly lower. 37% of the population have poor GCSEs, 23% experience psychological distress, 23% are obese, 10% are regular smokers, and 8% have poor self reported health (see Appendix Figure A2)

This outcome is not available at age 17 in the MCS but the value from age 14 is assumed to carry over to age 17.

Special education needs, Truancy and Exclusion are not measured at age 17 and are carried over from age 14, the total cost when excluding those three is £538

Calculated at birth and discounted at 3.5 percent a year.

This is due to increases in costs to the public associated this hospitalisation

The Treasury green book (MacLennan et al., 2021) suggests the value of a WELLBY is £13,000 with an upper limit of £16,000 and lower limit of £10,000. In which case the wellbeing gain can be valued between £2,828 million and £4,525 million. There is also the much lower supply side valuation of about £2,755 a WELLBY which values the WELLBY gain at £779 million.

We also present simulation estimates with SDQ internalising - the sum of emotional and peer problem scores - as the life satisfaction measure instead in Table A7. The increase in life satisfaction is about 30% lower for scenario 1 when using this measure.

It is likely undertaking a program like this will involve significantly more in administrative costs but we do not calculate them here.

They can also be considered as short-term effects from intervention studies that are then harmonised with and plugged into LifeSim.

from the point of view of LifeSim, they may be important human capital variables, outcomes that have significant costs to the public, wellbeing, etc.

We consider factors that have an effect on the measurement of the risk factor or outcome to also be a confounder, even if they have no effect on the “true” risk factor or outcome.

Income fifths are based on the distribution of household income within the multiply-imputed MCS data with age 3 UK population weights.

North East, North West, Yorkshire and the Humber, East Midlands, West Midlands, East of England, London, South East, and South West

White, mixed, Indian, Pakistani and Bangladeshi, Black or Black British, and other ethnic group (inc. Chinese and other Asian)

Measured by receipt of any disability benefits by either the main parent or partner.

This also includes moderators that can be considered a special type of “collider” that involves selection into the risk factor but does not involve “collider bias”.

In this paper we estimate the effect of income on five outcomes at age 17 (poor GCSEs, Kessler score, obesity, regular smoking, and self reported poor health) and ten outcomes through childhood and adolescence (SDQ emotional symptoms, SDQ conduct problems, SDQ hyperactivity, SDQ peer relationships, hospitalisation, truancy, exclusion, special educational needs statement, disability and cognitive ability). We believe that early childhood income affects each of these outcomes either directly or indirectly through effects to the cognitive ability, socio-emotional/ mental health, or physical health of the child. Two recent systematic reviews of the literature (Cooper and Stewart, 2021; Page, 2024), present evidence of the effect of income on cognitive ability. The studies they include show that an increase in income improved cognitive ability as measured by maths, reading and verbal test scores (Blau, 1999; Dahl and Lochner, 2012; de Gendre et al., 2021; Duncan et al., 2011; Fernald et al., 2008; Milligan and Stabile, 2011; Votruba-Drzal, 2006), improved cognitive development as measured by memory and visual integration (Fernald et al., 2008), improved academic performance in school (Black et al., 2014; Clark-Kauffman et al., 2003; Duncan et al., 2011; Elstad and Bakken, 2015; Gennetian and Miller, 2002; Votruba-Drzal, 2003) and increased years of schooling (Bailey et al., 2024; Bastian and Michelmore, 2018; Votruba-Drzal, 2006).

Similarly they present evidence of the effect of income on mental health measured in terms of socio-emotional development. Increasing income during early childhood improves the socio-emotional health of children (Blau, 1999; Dearing et al., 2006; Gennetian and Miller, 2002; Hamad and Rehkopf, 2015; Votruba-Drzal, 2006; Zachrisson and Dearing, 2015), improved engagement, and reduced inattention, anxiety and aggression (Milligan and Stabile, 2011).

There are fewer studies looking into the causal effect of early years income on health outcomes after birth. Despite a large number associational and descriptive research on the subject, the causal literature is still relatively sparse. Some of the literature looking at the specific physical health outcomes of interest finds no statistically significant effect during childhood but finds an effect in adulthood (Currie, 2009; Kuehnle, 2014). de Gendre et al. (2021) and Ko et al. (2020) find that early years income results in lower likelihood of hospitalisations, and Doyle et al. (2024) found a reduction in income lead to increases in hospitalisation. Baughman and Duchovny (2016) and East (2020) find that early years income increases leads to reduced likelihood of poor/fair health and increased likelihood of excellent health. Aizer et al. (2022) show that an increase in income leads to increases life expectancy, increases BMI (but not obesity) reduces probability of being underweight. East (2020); Ko et al. (2020) also find early years income leads to lower rates of developmental delay and reduced incidences of acute and chronic conditions up to age 3. Since we define disability as a long term illness that affects day to day activity we believe a reduction in chronic conditions will translate to a reduction in disability among the children as well. The most studied mechanism through which income affects physical health is nutrition, particularly for low income households, Milligan and Stabile (2011) provide evidence for this, they show a reduction in reports of children going hungry following an increase in income during early childhood.

Another indirect mechanism we also hope to capture is the indirect effects on the outcomes through effects on the parents, either by increasing their income beyond the transfers (Barr et al., 2022), improved parental mental health / reduction in stress (Jones et al., 2019), changes in parental behaviour (Bullinger et al., 2023; Jones et al., 2019; Votruba-Drzal, 2006).

Our estimates may also be affected by reverse causation, whereby serious developmental difficulties emerging in early childhood reduce parental income at ages 9 months, 3 and 5, rather than parental income affecting child development. For example, caring for a disabled young child might affect parents’ mental health, labour market participation, earnings or employment stability more than caring for a non-disabled child. This issue of reverse causation is potentially relevant to three early childhood outcomes measured at ages 3 and 5: disability, hospitalisation and emotional symptoms (our proxy for wellbeing). As a simple check on the potential magnitude of this bias, we repeat our simulation of these three outcomes using only parental income at 9 months as the risk factor and compare this with our base case simulation using five-year average income as the risk factor (see Table A1). The assumption underpinning our simple check is that population average parental income loss due to reverse causation will plausibly occur gradually over time, rather than taking immediate and full effect in the first nine months when (i) paid parental leave protections are in place for most parents, (ii) differential caring burdens may not yet have taken their full cumulative toll on many parents, and (iii) many early childhood developmental problems may not yet have manifested by 9 months. If reverse causation bias is materially important, the 9-month income measure should be less contaminated by it than the five-year average, since any channel through which emerging childhood developmental problems affect parental income, whether via employment changes or parental mental health, has had less time to operate by 9 months. The 9-month estimates should therefore show weaker associations with child outcomes at ages 3 and 5 than the five-year estimates if reverse causation is driving our results. Appendix table A13 presents estimates of the effects of both parental income measures on disability, hospitalisation and emotional symptoms at ages 3 and 5. We find that the estimated effects of parental income at 9 months are either higher than or the same as the estimated effects of five-year average parental income, though no difference is statistically significant. This suggests that reverse causation is unlikely to materially affect our estimates in this instance.

The current model uses parent-reported SDQ Emotional Symptoms as the primary measure of wellbeing as parent reported SDQ scores are available consistently across all current sweeps. Alternative wellbeing measures are available at ages 11, 14 (Wellbeing grid) and 17 (SWEMWBS) which we hope to use in the future at those ages and help map the SDQ scores to a better wellbeing measure for us to use at earlier ages.

An alternative that is available at all ages is parent-reported SDQ Internalising, the sum of SDQ emotional symptoms and Peer problems scales. We choose to use SDQ emotional symptoms instead of SDQ internalising for a few reasons. SDQ scores used in our model are parent-reported and therefore may not reflect the actual levels of each attribute but rather the level perceived by the parent. The relationship between the actual levels and parent-reported levels for peer problems may be less correlated than that for emotional symptoms for school-aged children. While we do not have a wellbeing measure, SDQ emotional symptoms scale is predictive of a number of outcomes that are closely related to wellbeing (such as mental disorders, school performance.) whereas the concepts associated with the peer problems scale are more tenuously associated with wellbeing.

A version of Table 1 with wellbeing measured by SDQ internalising instead of just emotional symptoms is presented in appendix table A7.

Of the cohort of 19,519 children in the MCS only 10,757 children provided any data at age 17, this is without accounting for incomplete responses to specific questions even in years they did participate. To deal with this attrition and missingness in the data we use multiple imputation. We believe this helps increase the statistical power and reduce bias in our estimation of effects.

We used chained equations to impute missing data back to the second sweep (age 3) of the MCS. We use the second sweep instead of the first as more than a thousand eligible households were added to the cohort in that sweep that were missed in the first sweep. We follow Villadsen et al. (2023) and include a number of the same auxiliary variables that are predictive of our outcomes at age 17 and earlier in the imputation to improve the accuracy of our estimates. These variables are from various sweeps and included child physical health, parental substance use, maternal mental health, and other household characteristics. We generate 30 datasets using multiple imputation. Post-imputation, the final sample used in our analyses consists of 15,380 cohort members.

To build our models we follow a set of rules, described below with examples of their application, so our models are credible, conservative, parsimonious and focused on population averages. The rules below are used in the current version of LifeSim Childhood, but may change in the future as we develop LifeSim further. We will follow the DAG reporting recommendations of Tennant et al. (2021) in future work and include detailed documentation for each DAG produced along with the code.

1. Credible: Confounder selection must be based on strong theoretical framework, scientific evidence and expert opinion. There must be a credible story that justifies why the variable is a well-founded confounder.

2. Conservative: We include confounders that are also partly mediators, even though this will remove part of the total causal effect. Similarly, we also include confounders that are also moderators.⁴⁰ That makes our approach conservative. However, we do not wish to be over-conservative by over-adjusting the total causal effect downwards by controlling for too many mediating effects. So we do not control for “partly confounding mediators” that we consider to be primarily mediators rather than confounders - i.e. we make a scientific judgement that the mediating impact is more important than the confounding impact. This requires a scientific judgement drawing on prior knowledge about the temporal sequence of events and, if necessary, the expected relative strength of the causal impacts and correlations. If there is doubt about whether a variable is “primarily” a confounder or a mediator then we do not include it in the base model but do in the “extra conservative” model as a robustness check.

   • E.g. 1 a “partly confounding mediator”: when examining the effect of having a teenage mother on school results at age 17 (GCSEs), it is unclear if maternal mental health (MMH) at age 9 months primarily a confounder or mediator. We judge it is primarily a mediator because we expect variation in MMH age 9 months to be strongly driven by having a baby, and the relevant timing of MMH for causing teen pregnancy is at least 2 years before that at conception, so even though MMH at 9 month may be correlated with MMH 2 years before, the confounding impact is expected to be less strong than the mediating impact.

   • E.g. 2 a “partly mediating confounder”. when examining the effect of having a teenage mother on school results at age 17 (GCSEs), we do control for smoking in pregnancy because this is a proxy for risky behaviour which may confound the teen pregnancy effect. This is debatable, however, insofar as teen pregnancy itself might be conceptualised as related to risky behaviour which partly relates to some of the social causal pathways from teen pregnancy to child outcomes. We therefore do not include this in our preferred model but do include this as a confounder in our “extra conservative” model. (A similar example is whether to control for IMD, which turns on whether pregnancy is more likely to cause the parents to move out of the grandparents house to a deprived neighbourhood, or whether living in a deprived neighbourhood is more likely to cause teenage pregnancy).

   • E.g. 3 a “confounding moderator”. When examining the effect of disability at age 3 on school results at age 17 (GCSEs), income between ages 0 and 5 is included as a confounder even though we expect it to have a moderating effect. This moderating effect is not explicitly modelled because we are not including interaction terms. We just want the population average effect.

3. Parsimonious: We prefer a simple model unless additional complexity is clearly justified and makes an important difference. As well as the general scientific virtue of keeping things as simple as possible but not simpler, parsimony in relation to confounder selection has the further advantage of reducing the variance of the effect estimate: adding further possible confounding variables that are not distinctive from the preferred set of confounding variables will tend to increase the variance of the effect estimate without improving its accuracy.

   1. Use a simple functional form with fewer parameters to estimate and interpret where possible.

   2. Exclude confounders that are not distinctive i.e. they are likely measuring the same thing as other confounders.

      1. A confounder is considered distinct if the causal pathway to either the risk factor or the outcome is distinct from other confounders. The causal pathway to both the risk factor and the outcome do not have to be distinct.

      2. When multiple options are available choose the measure most relevant for the causal pathway.

      3. E.g. when examining the effect of low birth weight on school results at age 17 (GCSEs), being a single parent could be a potential confounder as it could capture some economic characteristics of the household (it likely will not capture anything else, such as time with child because of exposure timing) that may affect birth weight and later education outcomes. However, we include household income and IMD as confounders and that should capture everything that single parent captures in this instance. This will not be the case if the exposure is disability at age 5.

   3. Exclude prior measurements of outcome and/or risk factor. We are not interested in modelling the effect of changes or the trajectory of outcomes by each sweep, we are interested only in the full direct effect.

      1. E.g. when examining the effect of cognitive ability at age 7 on wellbeing at age 17, we do not include measures of cognitive ability or wellbeing as confounders. We are currently interested in modelling the direct effect of a specific cognitive ability level on wellbeing and not on how changes in cognitive ability affects wellbeing or cognitive ability affects wellbeing trajectory.

      2. Note: An alternative approach to causal inference would be to include a prior measure of the risk factor as a control variable - for example, estimating the effect of income at age 5 controlling for income at age 3. However, we believe this would be an over-adjustment that would under-estimate the causal effect of the exposure level at T on the outcome level at T+1. Including a prior measure would estimate the effect of the exposure trajectory (first difference) rather than the effect of the exposure level which is our parameter of interest.

   4. Do not include both linear and non-linear forms of the same confounder. But the linear or non-linear measures can be used individually as appropriate for the model.

      1. E.g. when examining the effect of disability at age 3 on school results at age 17 (GCSEs), income between ages 0 and 5 is included as a confounder. Poverty between ages 0 to 5 is not currently included as a confounder as income and poverty are seen to capture the same causal pathway, even though those below the poverty line may have different effects for those above.

   5. For an outcome risk factor pair, the model used is specific to risk factor timing only. i.e. for a particular risk factor and outcome pair the same model should be used for outcomes at all ages as long as risk factor timing is constant. However if the risk factor timing changes the model should also change.

      1. E.g. when examining the effect of cognitive ability at age 7 on wellbeing, we use the same model to simulate wellbeing from ages 11 upto 17. However, if we want to examine the effect of cognitive ability at age 5 on wellbeing, we use a different model to simulate the effects on wellbeing from ages 7 to 17.

4. Focused on population averages Do not include interaction terms, since our primary interest lies in the unconditional population average effect rather than the moderating effects for sub-populations with specific levels of the moderating variable.

   1. E.g. when examining the effect of disability at age 3 on school results at age 17 (GCSEs), we do not include interaction between age 3 disability and parental income age 0-5, since we currently just want the population level effect of age 3 disability and not how this effect is modified by parental income.

The advisory group for the two grants from the Medical Research Council Prevention Research Partnership (“ActEarly Programme”, Grant # MR/S037527/1) and UK Research and Innovation (Grant # MMR/X002837/1) include those below. We are extremely grateful to all members of our advisory group for their support, though absolve them of responsibility for our methodological choices and errors.

Anna Freud: Jessica Deighton

Bradford Institute for Health Research: David Ryan, John Wright

Department for Education: Catherine Newsome

Department of Health and Social Care: Lucy Andrews

Department for Work & Pensions: Mike Daly

Institute for Fiscal Studies: Sarah Cattan

London School of Economics: Miqdad Asaria, Sara Evans-Lacko, Paul Frijters

Public Health England: Annalisa Belloni

The Behavioral Insights Team: Tom McBride

Tower Hamlets: Somen Banerjee

University College London: Nichola Christie, Peter Goldblatt, Heather Joshi, Catherine Law, George Ploubidis, Aase Villadsen

University of Dundee: Jan Boehnke, Louise Marryat

University of Essex: Patryk Bronka, Matteo Richiardi

University of Leeds: Mark Mon-Williams

University of Liverpool: David Taylor-Robinson

University of Oxford: Leon Feinstein

University of Sheffield: Sarah Bates, Alan Brennan

University of York: Karen Bloor, Jonathan Bradshaw, Richard Cookson, Tim Doran, Ruth Helstrip, Rowena Jacobs, Ruth Patrick, Kate Pickett, Ieva Skarda, Shrathinth Venkatesh

Young Person Representative: Brooke Johnson

Youth Futures Foundation: Andrea Barry

Figure A1

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Figure A2

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Figure A3

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This work was supported by the Medical Research Council Prevention Research Partnership ("ActEarly Programme", Grant # MR/S037527/1) and UK Research and Innovation (Grant # MMR/X002837/1).

We would like to thank all the many people who have contributed towards the development of LifeSim Childhood over many years, through discussions or comments on previous versions of the paper, including the anonymous reviewers, Lucy Andrews, Sarah Bates, Patryk Bronka, Adam Bricknell, Emma Brookes, Eric John Brunner, Sarah Cattan, Mary-Alice Doyle, Sara Evans-Lacko, Rowena Jacobs, Brooke Johnson, Isaac J Parkes, Liina Mansukoski, Emil Margrain, Laurie McClymont, Matteo Richiardi, Matthew Warburton, John Wright, Emir Zaidi, and seminar participants at Health Economics Study Group Meeting Summer 2024, University of Aberdeen, University of Leeds and University of York. We also thank participants of theMillennium Cohort Study for providing valuable data on their lives andexperiences.

1. Version of Record published: September 18, 2026 (version 1)

© 2026, Venkatesh et al.

This article is distributed under the terms of the Creative Commons Attribution License, which permits unrestricted use and redistribution provided that the original author and source are credited.