Universal Early Childhood Education and Care for Toddlers and Achievement Outcomes in Middle Childhood

Abstract

We estimated the effects of Norway’s universal ECEC program—expanding access to 1- and 2-year-olds starting in the early 2000s—on standardized math and achievement tests in 5th grade (age 10) using a population-based survey sample (Norwegian Mother, Father, and Child Cohort Study, MoBa, n = 102,352), linked with national administrative records of child achievement test scores. We used two methods to test the effects of attending ECEC: fixed-effects and instrumental variable regressions. Although both approaches found small and mostly insignificant main effects, the effect of ECEC is consistently stronger for children from families with low parental education. The fixed-effects analyses showed that ECEC reduced inequalities in achievement across levels of parental education by about 10% while the instrumental variable analyses, using variation in ECEC induced by the expansion, showed reduction of about 50%. These results suggest that expanding access to ECEC for toddlers has the potential to reduce achievement inequality.

Keywords:

• Early childhood education and care
• universal child care
• toddler care
• achievement
• instrumental variables
• fixed-effects
• MoBa

Universal publicly-funded Early Childhood Education and Care (ECEC) programs for preschoolers are implemented in many European countries, and also increasingly so in the US, where programs targeted at children from families with low income or facing other risk factors have been more common (Cascio, 2021). Proponents of universal ECEC argue—by avoiding confusion over the eligibility rules required for targeted programs and the stigma that can arise with programs focused on serving at-risk children only—that participation rates will be higher among children who can benefit most; that children from families with low income or otherwise at social risk gain from being in more diverse child groups; that families with higher incomes struggle to pay out-of-pocket for ECEC programs too and their children can also benefit from a high-quality early learning experience; that universal programs attract stronger public support; and that there is a stronger focus on program quality when socioeconomically advantaged children also attend (e.g., Barnett, 2010). In the US, most of the debate around effectiveness of ECEC, and of universal programs specifically, has focused on programs for preschoolers (Barnett, 2010; Farran, 2016; Phillips et al., 2017). However, recent policy proposals have introduced the idea of universal ECEC programs for toddlers as well (e.g., Warren, 2019). While controversial in the US, universal programs for 1- and 2-year-olds have been implemented in Northern Europe over the last decades (Dearing et al., 2018; OECD, 2006), and evidence on their achievement effects is expanding.

A meta-analysis of 27 quasi-experimental studies of universal programs in Europe and the US found overall positive short- and long-term effects, strongly driven by programs with high structural quality (in terms of staff education level and child:staff ratios), with effects most pronounced for socioeconomically disadvantaged children (van Huizen & Plantenga, 2018). These results are consistent with a recent narrative review on the same topic (Blau, 2021). Yet, evidence on longer-term effects of universal programs that begin in toddlerhood is scarce, as studies have mainly examined outcomes measured during or just after the end of the program for this age group (van Huizen & Plantenga, 2018). With concerns of fadeout (Bailey et al., 2017), this is currently a critical limitation in the literature.

In this article, we add to the literature by estimating the effects of universal ECEC beginning when children are toddlers, on national achievement tests when children are 10 years old (i.e., 5th grade), examining differential effects by family socioeconomic status indicators. To do so, we exploit the national expansion of universal ECEC in Norway that occurred during the 2000s. We use data from a national health survey, the Norwegian Mother, Father, and Child Cohort Study (MoBa; Magnus et al., 2016), covering the most crucial years of the policy expansion, linked with national registries on achievement outcomes, demographics, income, and residency, as well as public records on the proportion of the age group enrolled in ECEC.

The policy expansion leveraged to identify ECEC effects in this study has previously been used by Dearing et al. (2018). They found that the ECEC expansion reduced language gaps at age 3 between children from low- and high-income families. Their study, however, relied on parent-reported language outcomes at a very young age when children were still attending ECEC. To extend their analyses, we used national achievement tests that are not subject to parent-report bias (and attrition due to parent non-response) in addition to measuring outcomes many years after ECEC exposure. We found positive long-term effects of ECEC attendance on math and reading test scores in 5th grade for children from families with low levels of parental education, reducing achievement inequality by between 10 and 50%, depending on the analytical approach. ECEC effects were also found to vary by parental income, but the income interaction effects were less precise and consistent than those for parental education.

Effects of ECEC and Alignment with Children’s development

Meta-analyses have, quite consistently, shown targeted preschool programs—for 3 to 4-year-old children—to be effective in promoting preschool cognitive skills in the short run, with effect sizes averaging around 20–30% of a standard deviation (Camilli et al., 2010; Duncan & Magnuson, 2013). There is also some meta-analytic evidence of persistent effects throughout adolescence and early adulthood on outcomes such as grade retention and special education placement (McCoy et al., 2017). The same is true for universal preschool programs in cases where structural quality is high (i.e., high teacher: child ratios, educational requirements for teachers), with effects evident primarily among children from families with lower income and/or parental education (van Huizen & Plantenga, 2018).

There are, however, notable exceptions. Most prominent are quasi-experimental studies of Quebec’s scale-up of universal ECEC subsidies (Baker et al., 2008; Baker et al., 2019; Kottelenberg & Lehrer, 2017), covering children aged 0–4. These studies found mixed short- and long-term effects on cognitive- and academic outcomes (for example, negative effects of about 20% of a standard deviation of program exposure on a Canadian national test in math and reading for ages 13 and 16, yet with positive effects of about 10–30% for PISA math and reading scores; Baker et al., 2019). Consistent with effects of universal ECEC being conditional on quality (van Huizen & Plantenga, 2018), observed quality was low, especially among the youngest children, who primarily attended home care (Japel et al., 2005).

While the majority of universal ECEC programs in high-income countries include preschool-age children (aged 3 or 4), developmental scientists have long argued that the earliest years (ages 0–3) are foundational in terms of brain development and, thereby, cognitive and language development (e.g., Shonkoff & Phillips, 2000). Socioeconomic disparities in development are evident already during children’s earliest years, exemplified but not restricted to language development. In vocabulary learning and language processing at age 1½ and 2 years, children of parents with low levels of education in the US lag six months behind their counterparts with parents having higher levels of education (Fernald et al., 2013). This may in part be a function of exposure to language-enriched environments, which have been shown to be consequential for early brain development (Romeo et al., 2018). Socioeconomic differences in tests of preschool skills like vocabulary are evident as early as age 2 also in several European countries, including progressive welfare states like Norway and Germany. In Germany, these differences remain quite stable into school age (e.g., Passaretta & Skopek, 2018; Skopek & Passaretta, 2020). In Norway, they can be detected from age 2 (but not earlier; Ribeiro et al., 2022), and increase throughout school age (Sandsør et al., 2023). This evidence points to the value of intervening early thereby potentially preventing such differences from developing prior to school entry.

The theory of compensating environments (Sameroff & Chandler, 1975) suggests that children from families with low education and income levels are at greater risk than other children for growing up in family environments that provide less than adequate cognitive and social-emotional stimulation. High-quality ECEC environments are hypothesized to compensate by providing an environment outside of the home in which children can thrive. The development of foundational skills is then hypothesized to be foundational for further development, based on principles of “skills beget skills”—that the acquisition of later skills builds on earlier skills (Cunha & Heckman, 2008). In developmental science, this logic is expressed as developmental cascades, the cumulative consequences for development of experiences within different contexts over time (Masten & Cicchetti, 2010). Thus, early socioeconomic inequalities in skills may have lasting consequences for a child’s development. Early compensation, through for instance ECEC, could therefore place the child on a more favorable developmental pathway toward learning with lasting consequences.

Yet, evidence is much more scarce with regard to the effectiveness of ECEC programs that begin prior to the preschool years, compared to those that begin in preschool. Some of the evidence comes from correlational studies in contexts without universal access policies. For example, Dearing et al. (2009) used data from the National Institute for Child Health and Human Development Study of Early Child Care and Youth Development (NICHD SECCYD; National Institute for Child Health & Human Development Study of Early Child Care & Youth Development, 2000) to examine a range of available ECEC settings, including center-based, family daycare, and home care. This study found larger doses of high-quality ECEC (i.e., sensitive and stimulating caregiver-child interactions) closed test score differences between children from high- and low-income families in middle childhood. A subsequent study also found effects on income- and graduation gaps in early adulthood (Bustamante et al., 2022). While neither of these studies focuses exclusively on ECEC starting in toddlerhood, they demonstrate the potential for long-term positive outcomes for children growing up in low-income families.

While Dearing et al. (2009) and Bustamante et al. (2022) make considerable efforts to rule out selection bias in their analyses, Jaffee et al. (2011) show that there is a risk in non-experimental data that results may be biased by unobserved confounding. Using a different US dataset (National Longitudinal Survey of Youth), Jaffee et al. (2011) report positive associations between math and reading scores at ages 11–13 and entry into ECEC in the first year of life, as well as in the second and third years, with coefficients around 30% of a standard deviation. However, none of these associations were upheld when adding sibling fixed-effects in the models.

Strong evidence for causal effects of universal ECEC beginning in toddlerhood comes from a few experimental and quasi-experimental studies. All of these studies, except Corazzini et al. (2021; see below) include ECEC programs of quite high structural quality, in terms of teacher: child requirements and teacher training.

Duncan and Sojourner (2013) used results from a randomized study in the US to project whether a two-year, center-based early childhood education intervention (the Infant Health and Development Program, based on the comprehensive Abecedarian curriculum) could reduce income-based achievement inequality. The authors conclude that a universal program has the potential to reduce this by half up to age 8, with slightly smaller effects for a targeted program. In France Berger et al. (2021) found positive short-term effects on language at age 2 (30% of a standard deviation), of early subsidized ECEC attendance beginning at age 1 using season of birth as instrument in an instrumental variable (IV) analysis. They also found more behavioral problems. Interestingly, this study founds much smaller effects when using conventional regression analyses (about half the size), which can be explained by suppressors that bias the effects downwards in conventional regression models or treatment effect heterogeneity (elaborated on below). Thus, quasi-experimental methods do not always provide smaller effect estimates.

A study from Norway exploited a lottery allocating children to slots in public childcare (Drange & Havnes, 2019). Children assigned by the lottery started ECEC at approximately age 1, while those not assigned started, on average, 6 months later. Those starting early scored 16% and 11% of a standard deviation better in reading and math screening tests in first grade (age 6). Moreover, for children of parents with lower education, the effects were about 60% larger than the average effects, fully closing the differences observed between children from families with high- and low parental education in reading, while reducing it by 25% in math. Finally, an Italian study found positive effects on 5th-grade language test scores of ECEC attendance for toddlers, but only for children with immigrant backgrounds, and no effects on math scores (Corazzini et al., 2021). These authors exploited variations across municipalities over time in ECEC availability in an instrumental variable (IV) analysis, finding a treatment effect for immigrants of about 60% of a standard deviation. Because ECEC quality varied considerably in content and quality across municipalities, this study is limited to addressing effects of a national policy, rather than any particular program.

There are also two examples of studies exploiting policy reforms of expanding ECEC for toddlers to identify short-term effects of ECEC, with empirical strategies similar to one we use in the present study (IV). In Germany, Felfe and Lalive (2018) found the expansion of ECEC slots to improve language- and motor skills for boys and immigrant children at age 6 with about 20% and 33% of a standard deviation, respectively. In Norway, as mentioned, Dearing et al. (2018) used the same ECEC expansion and data source (MoBa) that we use in the present study, finding effects for toddlers. They reported effects on language skills at age 3 of 89% of a standard deviation for children from low-income families attending ECEC at age 1½, 31% for middle-income children, and 29% (not statistically significant) for high-income children.

Taken together, the evidence from across contexts and research designs seems to suggest that universal ECEC starting in toddlerhood (with sufficiently high quality) is effective in improving language, cognitive, and achievement-related outcomes in the short run. Also, these programs may have added achievement benefits for children from low socioeconomic backgrounds. Yet, evidence for persistence of such effects throughout school age is largely based on correlational studies. Fadeout is a concern with regard to ECEC and other early childhood interventions in general (Bailey et al., 2017). There are examples of convergence in achievement scores across school age between children who attended and those who did not attended preschool (Puma et al., 2012; Yoshikawa et al., 2016), as well as reversals of initial effects, eventually favoring children in the control group (Lipsey et al., 2018). The present study is therefore critical in, to our knowledge, being among the first to address persistent effects of universal ECEC for toddlers well into school age, and in particular to address the question of the potential for universal ECEC to close socioeconomic inequalities in achievement.

ECEC Policy and Scale-Up in Norway

Since the mid-70’s Norway has gradually scaled up universal, publicly-subsidized ECEC. The first large expansion was a result of the Kindergarten Act of June 1975, which greatly increased government funding for investment and operating costs, leading to a substantial expansion of ECEC coverage for 3- to 6-year-olds (Havnes & Mogstad [2011] for details). In the 1990s, Norwegian ECEC policy was focused on establishing federal regulations for quality of care (e.g., teacher educational requirements and an educational content framework) for both center-based care and family daycare (Ministry of Education, 2014). Meanwhile, ECEC for 1- and 2-year-olds gradually became a policy focus. In 2002, a mandate required Norwegian municipalities to provide access for this age group in ECEC centers and/or family daycare units, leading to an increasing number of ECEC slots for 1- and 2-year-olds. The 2002 mandate legally anchored the incremental progression toward universal access, and with this mandate, public spending increased while corresponding family fees decreased. A maximum fee for full-time care was introduced in 2004 (2750 NOK or ∼ USD 400/month, 2004 exchange rate) and lowered in 2006 (2250 NOK or ∼ USD 360/month, 2006 exchange rate). The maximum fee was lower for low-income households, and the sliding scales below the maximum fee varied at the discretion of municipalities. Driven primarily by the mandate and these additional policies, the national coverage rate of ECEC for 1- and 2-year-olds expanded from 38% in 2001 to 77% in 2009. The coverage rate is defined as the number of 1- and 2-year-olds enrolled in ECEC divided by the number of 1- and 2-year-olds in the municipality. ECEC centers were either publically or privately owned, but were funded in the same way by the government and part of the same application system for families. As shown by Dearing et al. (2018), the expansion of ECEC reduced use of parental care for children from low-income families, while alternative forms of out-of-home care (family daycare and unqualified care) remained quite stable. For children from middle- and low-income families, there was in general a decline in the use of all alternative modes of care throughout the expansion.

Progress toward universal access, however, varied considerably across municipalities due to a wide range of idiosyncratic local circumstances, which we exploit in an IV framework. Obstacles to increased ECEC slots were primarily due to: (a) lack of available spaces for building new centers, high building costs, and lack of available contractors (particularly for the major cities); (b) lack of qualified staff (particularly for the smaller municipalities); (c) concerns in some municipalities about “over-coverage” due to year-by-year variations in birth-rates and for some municipalities conservative predictions of demand; and, d) local concerns over the availability of long-term earmarked funding from the government (Rindfuss et al., 2007; Rindfuss et al., 2010; Asplan Virak, 2006, 2009). At the time, Norway had a two-tiered governing structure of 19 counties divided into 428 municipalities. In Figure 1, we show that the median coverage rate within municipalities in Norway increased from 41% of all 1- and 2-year-olds in 2002 to 76% in 2008 (the time span covered in our study), while the variability across municipalities was considerable. In 2002, municipalities at the 25th percentile had a coverage rate of 31%, while the 75th percentile was 53%. In 2008, these gaps had narrowed, with the 25th percentile being 69% and the 75th percentile being 82%. This disparity, leading to different rates of change in ECEC coverage over time across municipalities, is the basis for our key identification strategy, described in detail below.

Figure 1. Municipality-level variation in coverage of ECEC for 1- and 2-year olds, across years 2002–2008. The coverage rate is defined as the number of 1- and 2- year olds enrolled in ECEC divided by the number of 1- and 2- year olds in the municipality.

It is also worth noting that the expansion of ECEC for 1- and 2-year-olds occurred within the context of progressive Norwegian parental leave policies. During the expansion, parents received up to one year of paid leave, and as a result, few children entered non-parental care prior to 9 months of age. After parental leave, parents had a choice between enrolling their child in publicly subsidized ECEC or receiving cash benefits (approximately NOK 3.500/month, or ∼ USD 560/month using the 2006 exchange rate) for staying home with their children (Ministry of Children, Equality, & Social Inclusion 2014). Parents were eligible for cash benefits until the child turned 3, and could switch between ECEC and cash benefit at their own discretion.

In terms of quality regulations, several aspects of quality and content of Norwegian ECEC were, and still are, regulated at a national level. In the 2000s, structural quality regulations stipulated that at least 30–35% of the staff should be ECEC teachers (with a 3-year university college degree) and that there should be a leader with ECEC teacher education in each center. Adult:child ratios of 1:3 for those under 3 and 1:6 for those older were also recommended, but not enforced by law. In ECEC centers, most children under age 3 attended infant-toddler groups of about nine children with three staff, one of them a trained ECEC teacher. Yet, variations in group size and age composition were allowed as long as the staff requirements were met.

The pedagogical content was guided by a “Framework” curriculum plan with national guidelines regarding the values and purpose of ECEC centers, their curricular objectives, and educational approaches (Ministry of Education, 2006). The curriculum plan specified there to be stimulating verbal and non-verbal interactions in all everyday situations, age-appropriate use of learning materials, and a learning-rich environment that included work with symbols, books, and reading. The early childhood pedagogy inherent in the framework plan is aligned with the “Nordic model”, emphasizing play-based and child-centered learning. Instruction-based teaching is uncommon, and children spend considerable time playing outdoors year around.

Although Norwegian ECEC could be considered a national program, its implementation varied between ECEC centers within the limits of the legal requirements for structural quality and the “Framework” plan. Evidence of such quality variation in Norway is somewhat mixed. One study has indicated that structural quality standards mostly followed regulations and recommended standards for the period covered by the present study (Winsvold & Guldbrandsen, 2009), while others suggest that quality standards were not met in all centers across Norway (Brenna et al., 2010; OECD, 2015). Moreover, observed quality for more recent cohorts (than those covered by the present study) find that most classrooms meet only mediocre quality standards, as assessed with the ITERS-R (Harms et al., 2017), in particular concerning hygiene, safety, and access to play materials (Bjørnestad & Os, 2018). The authors found the highest mean score on the interaction quality subscale, which was rated to be quite good.

Present study

In the present study, we hypothesized that attending ECEC from the second year of life would improve math and reading achievements in 5^th grade. We also hypothesized that these effects would reduce inequalities in achievement between children from lower- and higher socioeconomic status backgrounds (i.e., low family income and/or lower levels of parental education). We took two complementary analytical approaches to address these hypotheses, each with distinct strengths and limitations.

We used birth cohort by municipality fixed-effects (FE) regressions and instrumental variables (IV) regressions. The FE regression is an efficient estimator for effects of ECEC on achievement outcomes exploiting all variability in ECEC use within a municipality-by-year cluster, hence estimating the average treatment effect (ATE) of attending ECEC, conditional on covariates. These analyses provide unbiased estimates of ECEC use under the assumption that ECEC use is as-random after accounting for a detailed list of child and family covariates and fixed effects. Our IV analyses provide a different estimate; the effect of ECEC use caused by the policy expansion, for children who respond to the expansion (compliers), known as the local average treatment effect (LATE). These analyses rely on a different set of assumptions (to be detailed below). We use municipality by cohort variations in availability of ECEC as an instrument for ECEC use. Assuming a strong and valid instrument, these models provide unbiased estimates of LATE, although less efficient than our FE regression estimates.

Methods

We used data from the Norwegian Mother, Father, and Child Cohort Study (MoBa; for complete details, see Magnus et al., 2016, and www.fhi.no/morogbarn; Magnus et al., 2006), a population-based pregnancy cohort study conducted by the Norwegian Institute of Public Health. Participants were recruited from all over Norway from 1999 to 2008. The full sample included 114,500 children, 95,200 mothers, and 75,200 fathers at baseline. The current study is based on version 12 of the quality-assured data files released for research in January 2019. For the present study, MoBa was linked (through person identification numbers) with Norwegian administrative records, provided by Statistics Norway. This study included all children in MoBa born in 2002–2008, resulting in a sample of 102,352 children. Of those invited to participate in MoBa, 41% agreed to participate. Yet, although all women giving birth in Norway were the target population, only hospitals and birth units with more than 100 births annually were included, and the roll-out of the study was gradual across the first years (Magnus et al., 2006). Analyses based on our linked data show that between 16.9% (in 2002) and 31.3% (in 2006) of all births in Norway were included in MoBa. In Appendix 1, we show the income and education distributions of families participating in MoBa, compared to the whole population of families with children born 2002–2008 (Figure S1 and Table S1, see description of measures below). As previously indicated (Magnus et al., 2006), families with lower income and low levels of education are under-represented in MoBa. However, the associations between achievement test scores in 5th grade, and income and education, respectively, are almost identical in the MoBa sample and the comparable population (see online Appendix 1).

Retention rates in MoBa were 78.1% at age 6 months and 66.4% at age 1.5. In the present study, we used data collected at 0.5 years (family-level covariates) and 1.5 years (child care use). The MoBa was linked to national registries covering the entire population, including the population registry (demographic information), the income registry (family income), and the education registry (parents’ education level and child test scores from national tests in 5th grade). Linkage, via person identification numbers, was available from the birth cohorts of 2002 and onwards.

The establishment of MoBa and initial data collection were based on a license from the Norwegian Data Protection Agency and approval from The Regional Committees for Medical and Health Research Ethics. The MoBa cohort is now based on regulations related to the Norwegian Health Registry Act. The current study was approved by The Regional Committees for Medical and Health Research Ethics. The data linkage with administrative records used in the present study was approved by The Regional Committee for Medical Research Ethics and the Data Protection officer at the first author’s host institution.

Measures

National test scores, 5th grade

Compulsory national assessments for children in 5th grade have been administered every fall in Norway since 2007, in the subjects reading (Norwegian), mathematics, and English (the first two included in the present study). Test development is commissioned by the Directorate of Education and Training and carried out by subject experts at universities in Norway along with psychometric experts in the Directorate (see https://www.udir.no/eksamen-og-prover/prover/nasjonale-prover). The tests are designed to capture the full range of subject skills among students in 5th grade. About 96% of all students in Norway take the test; students with special needs and those following introductory language courses may be exempt. Data from 2007 and onwards are available as a score summing up correct responses. In addition, from 2014 (for the 2004 and later cohorts), a scaled score based on a 2-parameter IRT model is available (for details, see https://www.udir.no/globalassets/filer/vurdering/nasjonaleprover/metodegrunnlag-for-nasjonale-prover-august-2018.pdf). In the present study, we standardized the summed test scores within year and conducted robustness checks with scaled scores.

ECEC Arrangements

Mothers reported the type of child care used at age 1.5 years, representing the child’s primary care arrangement. Choices included “at home with mother or father,” “at home with unqualified child minder,” “family day care,” and “center care.” From these reports, we computed a dummy variable indicating whether children were in center-based ECEC versus any of the other arrangements. Center-based ECEC was the target of the expansion, and is the policy-relevant focus given the recent discussions toward universal ECEC.

Municipality-Level ECEC Coverage

For our instrumental variable analyses, we used municipality-level ECEC coverage rates as an instrument. Coverage rates were derived from public records of the total ECEC coverage for children aged 1 and 2 in municipalities by year (https://www.ssb.no/en/statbank/table/12562/). Because the municipalities fund public ECEC, these public records are accurately representing the availability of ECEC. We link municipality by year coverage rate to children via the child’s residential municipality at age 1.

Household Income and Family Education

We combined the after-tax income for each parent, averaged across the year of the child’s birth and the prior year, and adjusted incomes to 2018-levels of the consumer price index. The lowest 2% of annual incomes (in the population) were set to missing and imputed (see description of imputations below) because very low or negative incomes can indicate that losses from private companies have been deducted on the tax records rather than their reported income being low. Moreover, incomes were truncated at the 98th percentile to remove the influence from outliers. We then centered it at the lowest observed income (approximately NOK 13,000, or USD 1,600, 2018 average exchange rate) and divided it by 100,000.

For the municipality-level analyses (as part of instrument validation, see below), we calculated a ratio of family income-to-needs to account for variations in family size. For each child across the three first years of life, we divided total after-tax income by the OECD poverty line for each particular year (50% of the median income, adjusted for family size; OECD, 2011).

The highest family education was drawn from the education registry, recording the highest completed level of education for mothers and fathers. We converted the ordinal scale into years of education, following the standard guidelines from Statistics Norway. We defined the family education variable as the highest value of either the mother’s or father’s education. For analyses, we centered education on 9 years (i.e., completed compulsory schooling), which is the lowest common level of education.

Covariates

Our choice of family and child covariates was primarily informed by previous research on selection into ECEC in Norway (Sibley et al., 2015; Zachrisson et al., 2013). From the registries, we include demographic information: Child gender; Maternal age (in years, truncated at 3rd and 97th percentile); Child age at testing; Immigrant status: one western immigrant indicator (0, 1) for being born or having at least one parent born in Europe (except Norway), North America, or Oceania, and one non-western immigrant indicator (0, 1) for being born or having at least one parent born in the rest of the world (except Norway); Number of children in the household (count of household members < =18 years as an average across the child’s first 3 years of life, truncated at 4. i.e., the 99th percentile); Number of adults in the household (count of household members >18 years in child’s first year); and birth month dummy variables. From the Medical Birth Registry, we included birth weight (dichotomized [0.1]: <2500 and ≥2500 grams), Apgar score (five minutes after birth), and multiple birth (i.e., twins). From MoBa, we included mothers’ report on their anxious/depressive symptoms (Tambs & Moum, 1993) and partner/spouse relationship satisfaction (Rosand et al., 2011) when children were 6 months old.

For selected covariates, we compute aggregated municipality-by-year-level covariates based on all families within a municipality-by-year cluster with a child aged 1 for the instrument validation (see details below). These aggregated variables included proportion of families with (1) less than 12 years of education; (2) more than 16 years of education; (3) low income (at or below the 10th percentile); (4) high income (at or above the 90th percentile); (5) western- and non-western immigrants. A few small municipalities have extreme univariate outliers on the demographic variables. Therefore, we capped these aggregate variables at the 98th percentile of the municipality-weighted distribution.

Statistical Analyses

Birth Cohort by Municipality Fixed-Effect Regressions

The FE regressions estimate the ATE of attending ECEC, conditional on covariates. The counterfactual outcome (test scores) for children attending ECEC by age 1½ is the what-if outcome had they not attended ECEC by this age, regardless of whether (or when) they eventually entered ECEC. In other words, the counterfactual condition includes children entering ECEC at any time after age 1½ (i.e., between 19 and 60 mo) or never entering ECEC (the latter being rare). In the FE models, we estimate the effects of ECEC on the outcome by conditioning on covariates (W) and municipality ($\alpha$) and cohort ($\gamma$) fixed effects, where $i,$ $m,$ and $c$ index individual, municipality, and cohort: (1) $${\mathit{Outcome}}_{\mathit{imc}}= {\alpha }_m+{\gamma }_c+{\beta }_1{\mathit{ECEC}}_{\mathit{imc}}+ {\beta }_2{W}_{\mathit{imc}}+{ϵ}_{\mathit{imc}}$$(1)

The covariates included all child- and family variables listed above and shown in Table 1 (also education and income), and indicators for birth month (to account for the main uptake in ECEC in August). After estimating the main effects of ECEC use, we included product terms that allow the estimated effects of ECEC to vary by family income and family education. (2) $${\mathit{Outcome}}_{\mathit{imc}}= {\alpha }_m+{\gamma }_c+{\beta }_1{\mathit{ECEC}}_{\mathit{imc}}+ {\beta }_2{\mathit{SES}}_{\mathit{imc}}{ + \beta }_3{\mathit{ECEC}}_{\mathit{imc}}\mathrm{*}{\mathit{SES}}_{\mathit{imc}}+ {\beta }_3{W}_{\mathit{imc}}+{ϵ}_{\mathit{imc}}$$(2)

Table 1. Descriptive statistics. MoBa data (N = 102,983).

	% Missing	M(SD)/%	Min-Max
Achievement 5^th grade
Math (unscaled)	5.77	0.18 (0.98)	−2.98 − 2.36
Reading (unscaled)	4.63	0.18 (0.98)	−3.08 − 2.20
Math (scaled – from 2004)	8.55	51.95 (9.54)	19.36 − 79.66
Reading (scaled – from 2004)	9.59	51.94 (9.49)	18.45 − 75.68
ECEC
18 months	33.00	52.97%
Socioeconomics
Family income (NOK 100,000’s)	0.03	6.68 (2.10)	0.36 − 17.86
Family education (highest)	5 56	14.37 (2.68)	0.00 − 23.00
Family characteristics
Non-western immigrant	0.00	4.73%
Western immigrant	0.00	9.51%
Maternal age	0.00	30.65 (4.55)	20.00 − 40.00
Maternal anxiety/depression	22.56	1.24 (0.35)	1.00 − 4.00
Relationship satisfaction	25.26	5.26 (0.73)	1.00 − 6.00
Number of children	0.00	1.79 (0.83)	1.00 − 4.00
Number of adults	0.00	1.83 (0.32)	0.33 − 4.33
Child characteristics
Boy	0.00	51.27%
APGAR 5 min	0.12	9.41 (0.84)	0.00 − 10.00
Low birth weight	0.05	4.45%
Twin birth	0.00	3.35%
Birth month (average)	0.00	6.40 (3.35)	1.00 − 12.00
Birth cohort
2002	0.00	9.08%
2003	0.00	13.04%
2004	0.00	13.94%
2005	0.00	15.89%
2006	0.00	17.76%
2007	0.00	16.51%
2008	0.00	13.77%

Following recommendations by Duncan and Magnuson (2003), our primary analyses included modeling interactions with parental income and education separately, under the assumption that these moderately correlated indicators of socioeconomic indicators (0.38 in our data) capture financial and human capital differentially. As a robustness check, we also included them simultaneously.

The FE regression models are based on the assumption that after accounting for observed family and individual characteristics, outcomes of children who entered ECEC after 18 months of age (or never entered ECEC) can serve as a counterfactual for the children who attended ECEC by 18 months within the same municipality by birth cohort group. While these FE regression models provide an efficient estimator of the treatment effect, we must still be concerned about unobserved family selection factors occurring within municipality. We probed the omitted variable risk by testing the robustness or fragility of our estimates in supplementary sensitivity analyses, using the coefficient of proportionality method (as described in Dearing & Zachrisson, 2019; Oster, 2019). This method indicates of how large the impact of unobserved selection factors would need to be relative to unobserved variables to nullify our FE regression results. Sensitivity analyses are agnostic with regard to the direction of bias. Results that are fragile—highly sensitive to potential omitted variable bias—are sensitive to being affected in either a positive or negative (upward or downward) direction by omitted sources of bias (i.e., if a model is sensitive to omitted variable bias, not including that source of bias could just as easily be leading to downwardly biased estimates as upwardly biased estimates).

Instrumental Variable Regressions

In our second set of analyses, we estimated two-stage least squares IV regression models with municipality and cohort fixed effects. Our instrument was the coverage rate of ECEC in each of Norway’s municipalities in each of the study years. Hence, variation in our instrument is time by municipality variation in ECEC coverage. In these models, the counterfactual is the outcome (test scores) for children had they not attended ECEC by age 1½, for those who start ECEC by age 1½ because of the policy expansion. Hence, our IV analyses provide a different estimate than the FE models; the effect of ECEC use caused by the policy expansion, for children who respond to the expansion (compliers), known as LATE. There were considerable differences between municipalities in the extent to which coverage increased across the time period 2002–2008 (Figure 1). In Figure 2 below, we illustrate the differences in rates of change. We graph four groups of change rates in ECEC coverage, created by subtracting the within-municipality coverage in 2008 from that in 2002, and then splitting the rate of change into quartiles. From 2002 through 2008, the median increase in coverage was 34.2 percentage points, while the 25 percentile was 23 percentage points and the 75 percentile was 43 percentage points.

Figure 2. Changes in municipality-level ECEC coverage rate averaged for municipalities within quartiles of change (from those with the lowest change rate [starting on top] to the highest [starting at the bottom]).

The first and second stages of our IV models are shown in Equations (3)(3) $${\mathit{ECEC}}_{\mathit{imc}}= {\alpha }_m+{\gamma }_c+{{\beta }_1\mathit{ProportionECEC}}_{mc}+{\beta }_2{W}_{\mathit{imc}}+{\upsilon }_{\mathit{imc}}$$(3) and (4)(4) $${\mathit{Otcome}}_{\mathit{imc}}= {\alpha }_m+{\gamma }_c+{\beta }_1{\mathit{ECEC}}_{\mathit{imc}}^{\prime }+{\beta }_2{W}_{\mathit{imc}}+{\mu }_{\mathit{imc}}$$(4) below. In the first stage (Equation (3)(3) $${\mathit{ECEC}}_{\mathit{imc}}= {\alpha }_m+{\gamma }_c+{{\beta }_1\mathit{ProportionECEC}}_{mc}+{\beta }_2{W}_{\mathit{imc}}+{\upsilon }_{\mathit{imc}}$$(3) ), ECEC use was regressed on our instrument (i.e., the ECEC coverage rate in the corresponding cohort by municipality cluster for child i) and our covariate set (W). In the second stage (Equation (4)(4) $${\mathit{Otcome}}_{\mathit{imc}}= {\alpha }_m+{\gamma }_c+{\beta }_1{\mathit{ECEC}}_{\mathit{imc}}^{\prime }+{\beta }_2{W}_{\mathit{imc}}+{\mu }_{\mathit{imc}}$$(4) ), the outcomes were regressed on predicted values of ECEC from the first stage ($\mathit{ECE}{C}_{\mathit{imc}}^{\prime }$) in addition to covariates. (3) $${\mathit{ECEC}}_{\mathit{imc}}= {\alpha }_m+{\gamma }_c+{{\beta }_1\mathit{ProportionECEC}}_{mc}+{\beta }_2{W}_{\mathit{imc}}+{\upsilon }_{\mathit{imc}}$$(3) (4) $${\mathit{Otcome}}_{\mathit{imc}}= {\alpha }_m+{\gamma }_c+{\beta }_1{\mathit{ECEC}}_{\mathit{imc}}^{\prime }+{\beta }_2{W}_{\mathit{imc}}+{\mu }_{\mathit{imc}}$$(4)

Our covariate set included all individual-level variables used in the previous models. Finally, as with the previous models, we tested interactions with family income and parent’s education. For the IV models, we followed the simultaneous equation setup from Wooldridge (2010); the treatment and the instrument were multiplied with the moderator, and both interaction terms were included in the estimated models. Thus, we have two first-stage equations, one for the main effect of the treatment and one for the product of the treatment and the SES indicator. In each of the first-stage regressions, the covariate list includes the instrument, the product of the instrument and the SES indicator, and the observed covariates (Equations (5)(5) $${\mathit{ECEC}}_{\mathit{imc}}= {\alpha }_m+{\gamma }_c+{{\beta }_1\mathit{ProportionECEC}}_{mc}+ {{\beta }_2\mathit{ProportionECEC}}_{mc}\mathrm{*}{S\mathrm{E}S}_{\mathit{imc}}+{\beta }_3{W}_{\mathit{imc}}+{\upsilon }_{\mathit{imc}}$$(5) and (6)(6) $${\mathit{ECEC}}_{\mathit{imc}}\mathrm{*}{\mathit{SES}}_{\mathit{imc}}= {\alpha }_m+{\gamma }_c+{{\beta }_1\mathit{ProportionECEC}}_{mc}+ {{\beta }_2\mathit{ProportionECEC}}_{mc}\mathrm{*}{\mathit{SES}}_{\mathit{imc}}+{\beta }_3{W}_{\mathit{imc}}+{\upsilon }_{\mathit{imc}}$$(6) ). The second stage is the outcome regressed on the predicted values from these two equations as well as covariates (Equation (7)(7) $${\mathit{Outcome}}_{\mathit{imc}}= {\alpha }_m+{\gamma }_c+{\beta }_1{\mathit{ECEC}}_{\mathit{imc}}^{\prime }+ {\beta }_2{\left({\mathit{ECEC}}_{\mathit{imc}}\mathrm{*}{\mathit{SES}}_{\mathit{imc}}\right)}^{\prime }+{\beta }_3{W}_{\mathit{imc}}+{\mu }_{\mathit{imc}}$$(7) ). (5) $${\mathit{ECEC}}_{\mathit{imc}}= {\alpha }_m+{\gamma }_c+{{\beta }_1\mathit{ProportionECEC}}_{mc}+ {{\beta }_2\mathit{ProportionECEC}}_{mc}\mathrm{*}{S\mathrm{E}S}_{\mathit{imc}}+{\beta }_3{W}_{\mathit{imc}}+{\upsilon }_{\mathit{imc}}$$(5) (6) $${\mathit{ECEC}}_{\mathit{imc}}\mathrm{*}{\mathit{SES}}_{\mathit{imc}}= {\alpha }_m+{\gamma }_c+{{\beta }_1\mathit{ProportionECEC}}_{mc}+ {{\beta }_2\mathit{ProportionECEC}}_{mc}\mathrm{*}{\mathit{SES}}_{\mathit{imc}}+{\beta }_3{W}_{\mathit{imc}}+{\upsilon }_{\mathit{imc}}$$(6) (7) $${\mathit{Outcome}}_{\mathit{imc}}= {\alpha }_m+{\gamma }_c+{\beta }_1{\mathit{ECEC}}_{\mathit{imc}}^{\prime }+ {\beta }_2{\left({\mathit{ECEC}}_{\mathit{imc}}\mathrm{*}{\mathit{SES}}_{\mathit{imc}}\right)}^{\prime }+{\beta }_3{W}_{\mathit{imc}}+{\mu }_{\mathit{imc}}$$(7)

To address instrument validity, we followed the analytical strategies of Cornelissen et al. (2018), who used a similar ECEC expansion instrument. The first assumption is that the policy expansion causes variation in the probability for treatment, conditional on covariates (i.e., instrumental relevance). We find this to be the case; the instrument was strongly associated with our treatment, with the first-stage F-test of the instrument being highly significant (F[1, 699.60] = 192.06), and where a 10 percentage point increase in coverage was associated with a 4 percentage point higher rate of ECEC use on average across municipality and cohort clusters, conditional on covariates. This relatively strong first-stage in a just identified (i.e., one instrument) IV model reduces the risk of bias in the second stage, given that the instrument is otherwise plausibly random (Angrist & Kolesár, 2021).

The second assumption is that the instrument must be independent of the error term of the outcome, conditional on covariates and the municipality and cohort fixed effects. This assumption can be further separated into the ignorable treatment assignment assumption—unobserved variables do not confound the effects of the instrument on the outcome—and the exclusion restriction assumption—the instrument influences the outcome only through the treatment (Angrist et al., 1996). Our main logic is that we restrict our estimates to be within municipality to exploit this within-municipality variation. Without municipality and cohort fixed effects, these assumptions would probably not hold; municipalities or cohorts with high coverage rates may differ from units with low coverage rates in several ways. For example, urban areas have higher ECEC coverage rates than rural areas and urban area children typically have higher test scores (net of observed family characteristics, i.e., ignorable treatment assignment does not hold). We include municipality and cohort fixed effects in the IV model to account for such potential bias.

We tested this second assumption by following the strategy outlined by Cornelissen et al. (2018). A concern could be that the ECEC expansion would be different across municipalities that differed across a range of demographic characteristics. If the expansion was associated with these differences, they could also be correlated with the error term. To test this, we regressed the change in ECEC coverage between 2002 and 2008 on initial coverage in 2002. As can be seen in Table S3, first column, the change in coverage was strongly negatively related to the coverage rate in 2002. To test whether other municipality characteristics were associated with the expansion, we added a number of baseline (2002) municipality-weighted characteristics for the entire child population, the municipality size, and the fraction of children in the municipality participating in MoBa to the regression model. The set of covariates did not affect the association between initial coverage in 2002 and change in coverage from 2002 to 2008, and none of the municipality-level covariates in 2002 were significantly related to coverage that year. A joint significance test for the full set of covariates (except ECEC coverage in 2002) was null (p=.34). This supports the notion that from the onset, the expansion we are exploiting is unrelated to municipality characteristics. Moreover, ECEC coverage in the first year of our time window (2002) was not correlated with either of the outcomes measured that year, nor to municipality level pre-trends in test scores (not shown).

As an additional assessment of the second assumption (i.e., instrument is independent of the error term), we tested covariate balance for the instrument. While observed covariates are controlled for in the analyses, and hence will not bias the estimate, we would be more concerned about imbalance on unobserved variables if there were an imbalance on observed variables. To check this, we regressed our ECEC coverage instrument on municipality-level aggregated covariates. Three of the municipality-level covariates were significant, although not in a systematic manner, i.e, were not consistent with specific biases affecting the instrument. Coverage was higher in municipalities with higher proportion of low family education, higher proportion of high-income families, and higher proportion of children within the municipality participating in MoBa (Table S4). Moreover, our instrument was not unbalanced with regard to income or education at the individual level (nor any other covariate except for maternal age). Yet, we supplemented the balance test by substituting the treatment (ECEC use) in the first stage equation with income and education, respectively, to test whether the multivariate combination of ECEC coverage and other covariates predicted these outcomes (not shown). In both cases, F-values were below 0.5, which indicates that ECEC coverage and the covariates in combination are associated with income and education to a negligible degree. In sum, our assumption tests provided consistent support for interpreting our IV estimates of ECEC effects as causal.

Missing Data

Despite nearly complete data on key indicators such as family income and child test scores, there was considerable missing data due to attrition for ECEC use: 33% of children were missing ECEC data at 1.5 years. Although likelihood of having missing values on the study covariates was by and large unrelated to the treatment of interest, likelihood of attrition was slightly higher for more socially disadvantaged families. To account for this attrition, our statistical models were estimated using multiple imputation with 20 datasets for missing values, combining estimates and standard errors according to Rubin’s Rules (Rubin 1987). Our imputation models included both achievement measures and child- and family-level covariates listed in Table 1, in addition to the municipality-level covariates described above. All models were estimated using complete data only (listwise deletion) as a sensitivity check.

Results

Descriptive statistics can be seen in Table 1, including rates of missing data. Here is worth noting a few descriptive aspects of the key variables in our study. With regard to our treatment of interest, across all years, about 53% of children in the sample attended ECEC by 18 months. With regard to our moderators of interest, average (after tax) family income was NOK 663,000, in 2018 values (median income in 2019 for couples with children ages 0–7 was NOK 822,700, and for single parent with children 0–17, NOK 438,400; Statistics Norway, 2021), and average highest family education was 14.37 years (SD 2.68).

Estimating the Effects of ECEC on Achievement

Our primary results from both the FE regression and IV models are presented in Table 2. We first explain the FE regression results and then turn to the IV results.

Table 2. Fixed effects- and instrumental variable regression estimates of ECEC at 18 months on 5th Grade Test Scores, for 2002–2008 Cohorts (n = 102,346) using multiple imputed data (n = 20).

	Fixed-effects		Instrumental variable
	Math	Reading	Math	Reading
	Est. (se.)	Est. (se.)	Est. (se.)	Est. (se.)
ECEC main effect	0.026 (0.008)**	0.014 (0.007)^†	0.215 (0.135)	0.237 (0.137)^†
Interactions w/income
ECEC	0.066 (0.021)**	0.057 (0.022)**	0.441 (0.135)**	0.339 (0.117)**
Income	0.043 (0.003)***	0.018 (0.003)***	0.060 (0.009)***	0.021 (0.010)*
ECEC × Income	−0.006 (0.003)*	−0.007 (0.003)*	−0.042 (0.014)**	−0.019 (0.014)
Interactions w/education
ECEC	0.072 (0.016)***	0.057 (0.016)***	0.425 (0.125)**	0.435 (0.127)**
Education	0.081 (0.002)***	0.078 (0.002)***	0.098 (0.007)***	0.093 (0.007)***
ECEC × Education	−0.008 (0.003)**	−0.008 (0.003)**	−0.048 (0.009)***	−0.045 (0.009)***

Note: Covariates in all models are: child gender, APGAR 5 min, low birth weight, twin births, highest family education, family income, maternal age, number of children and adults, western- and non-western immigrant status, maternal anxiety and depression, maternal relationship satisfaction, birth month, cohort indicators. ^†p<.1, *p<.05, **p<.01, ***p<.001.

Birth Cohort by Municipality Fixed Effect Regressions

The left-hand panels in Table 2 provide results from fixed effect regression analyses. Although excluded from the table for brevity, the full set of covariates listed in Table 1 was estimated in these models (also, due to restrictive publication policies by the MoBa, we are not allowed to report coefficients for covariates). In the first row of Table 2, we report results from models regressing math and reading 5th^-grade test scores on ECEC use. In the remaining rows, we report interactions between ECEC and both family income and parent education.

In these models, the effect of ECEC was statistically significant for math scores (p<.01), but above conventional significance levels for reading scores (p=.07). In terms of effect size, children attending ECEC at age 1½ had, on average, 2.6% of a standard deviation higher scores on math, compared to children not attending ECEC at that age. In comparison, this difference was about 1.4% of a standard deviation for reading scores.

Turning to the interaction effects, we found that ECEC was most strongly associated with both outcomes (p<.05) for children from families with the lowest incomes. For these children, attending ECEC was associated with 6.6% and 5.7% of a standard deviation higher test scores in math and reading, respectively. For every additional NOK 100,000 in family income, the association with ECEC decreased by 0.6 and 0.7% of a standard deviation (for math and reading, respectively). Moreover, the estimated effects of ECEC on both math and reading were moderated by parent education: test scores were more strongly and positively associated with ECEC use for children from homes with lower levels of education. Among children of parents with 9 years of education, those attending ECEC scored 7.1 and 6.2% of a standard deviation higher in math and reading than those not attending. For each additional year of parental education, this effect decreased by .08% of a standard deviation for math, and by .09% of a standard deviation for reading. When we estimated the interactions with parental income and education jointly in one model, only education remained unchanged in terms of effect size and statistically significant.

The marginal effects of ECEC by varying levels of parental education (holding all other covariates at their mean values), are displayed in Figure 3, with the horizontal lines representing 20% of a standard deviation (i.e., the math standard deviation is 9.5). For example, ECEC reduces the expected test score difference between children of parents with 9 versus 18+ years of education by approximately 10%.

Figure 3. Test scores for math for children attending and not attending ECEC by levels of parental education, results from fixed effects regression analyses. The Y-axis is converted to scaled test scores.

In terms of practical significance, we rely on the translation of test scores into months of learning presented by Sandsør et al. (2023), based on Norwegian registry data. They used IRT-scaled test scores of identical tests given in 8th and 9th grade to estimate one year of unconditional learning gain to be equivalent to 36% of a standard deviation improvement. By using this as a rough indicator, the main effect for math (2.6% of a standard deviation) is equivalent to less than a month of learning. Yet, when considering the effect of ECEC for children of parents with 9 years of education, it is equivalent to about two months.

When we tested how sensitive our fixed effects regression analyses were to unobserved selection bias—following the strategy outlined by Dearing and Zachrisson (2019) and Oster (2019)—they appeared fragile and potentially altered by even weak omitted variable bias. Specifically, in examining the amount of unobserved selection bias it would take to nullify our findings, we find that unobserved confounders as little as 6–12% as powerful as our observed covariates could nullify our findings in these models. Despite having a rich set of covariates, they explain very little of the selection into ECEC (about 7%). To probe the direction of the potential omitted variable bias, we estimated the main effect models without family income and parental education as covariates, as well as without any covariates except birth month. Effect sizes were larger (with similar standard errors) in both cases. If omitted variables bias our estimates from the full model in the same direction, this suggests that we potentially overestimate the effect of ECEC.

Instrumental Variable Regressions

The right-hand panels in Table 2 report results from our IV regressions. These IV models also included the full set of covariates listed in Table 1. For the main effects of ECEC, the treatment effects were 21.5 and 23.7% of a standard deviation for math and reading, respectively, yet with large standard errors yielding statistically insignificant results.

With regard to interactions in the IV models, we found evidence of differential effects of ECEC by family income for math but not reading. Children of parents with the lowest observed income level scored 44.1% of a standard deviation higher in math if they attended ECEC compared to those who did not. For each additional NOK 100,000 (about USD 12,000) earned by the parents, this effect decreased by 4.2% of a standard deviation.

In addition, we found differential effects of ECEC use across levels of family education on both math and reading. These were largest for children of parents with 9 years of education: children who entered ECEC by age 1½ had math scores 42.5% of a standard deviation higher and reading scores 43.5% of a standard deviation higher than those who were not in ECEC by this age (p<.01 in both cases). For each additional year of parental education, the ECEC effect decreased by 4.8% and 4.5% of a standard deviation (p<.001) for math and reading, respectively. Following our rough translation of effect sizes into months of learning outlined above, the treatment effect for children of parents with 9 years of education is more than a year. When including interactions of ECEC with both income and education in one model, the interaction with income was reduced by more than 50% and no longer significant, while the interaction with education remained unchanged (not shown). Therefore, we only graph the interaction with education below.

The marginal effects of ECEC attendance on scaled test scores at varying levels of parental education can be seen in Figure 4 (again with mean levels of all other covariates), with the horizontal lines representing 20% of a standard deviation. Considering the point estimates, the differences in test scores between children of parents with nine versus 18+ years of education are about 50% smaller for children attending ECEC. The figure also shows that the marginal effects are not statistically significant at a 5%-level for children of parents with 13 years of education and above.

Figure 4. Test scores for math for children attending and not attending ECEC by levels of parental education, results from instrumental variable analyses. The Y-axis is converted to scaled test scores.

Robustness Checks

We conducted several robustness checks for these analyses. Complier analyses (reported in Appendix 3) found no subgroups across any covariate strikingly more likely to respond to the instrument than others. Moreover, for both fixed effects regressions and instrumental variable analyses, we found the results to be substantively identical when: (a) using complete data only (i.e., listwise deletion), (b) restricting analyses to first-born children only (approximately 45,000 children; second-born children with a sibling in ECEC can receive ECEC slot priority, and thus having an older sibling in care could have influenced the selection process), and (c) using the scaled test scores for math and reading, available for the 2004 through 2008 cohorts. These robustness checks are detailed in Supplementary Appendix 4, Table S6.

Discussion

To our knowledge, this is the first large-scale study examining whether universal ECEC beginning in toddlerhood has long-term effects. We document persistent effects on achievement well into school age for children from families with lower levels of education, and less robust effects for children from families with lower income. Our analyses are based on a unique combination of survey and administrative data, covering a time period with a sharp increase in the availability of ECEC for toddlers.

While the FE and IV are different estimands and not directly comparable, they are consistent in terms of identifying the strongest treatment effects primarily concentrated among children from families with lower levels of education. The IV estimates are considerably larger, but also much less precise. Such differences are often seen in the literature. For example, Berger et al. (2021) reported effect sizes about half the size in conventional regression analyses compared to IV analyses, while standard errors were about 7 times smaller in the regression analyses.

We see three potential reasons as critical to understanding why the two estimators may differ in size. First, it is important to consider that the FE and IV models address substantively different underlying questions. The FE regressions provide a comparison of all children in the sample who were attending ECEC at age 1½ versus all children in the sample not attending ECEC at age 1½, regardless of whether their attendance was driven by the policy expansion. In contrast, the IV estimates are restricted to a comparison of children directly affected by the rate of policy expansion within their municipality. That is, children who entered ECEC at age 1½ due to the policy expansion are compared with children who were not in ECEC by that time, but who would have entered ECEC if the policy expansion had reached them. That is, children who did not attend ECEC given their birth cohort by municipality placed them in a limited ECEC access context, but who would have attended ECEC by age 1½ if living in a high-access context due to expansion.

One key characteristic of the IV model is that it leverages variation in the treatment caused by the instrument. Some children are induced by the instrument (compliers), while others are not (never takers and always takers). If compliers are affected more by ECEC than other children, then that could be one explanation for the larger effects in the IV analyses. We probed this explanation by looking at background characteristics for compliers but did not find any striking differences between the complier group and the full sample. Nevertheless, we found stronger treatment effects among compliers than in the full sample. This may be true even though we were unable to identify specific characteristics of the complier group.

A second potential explanation—that is not mutually exclusive with the first possible explanation—is that the strong treatment effect among compliers could be a function of how the policy expansion affected age of entry into ECEC. In both cases (FE and IV), the comparison group includes children who entered ECEC at any point after age 1½, as well as children who never entered (although the latter group is very small). We speculate that some of the difference between the IV and FE estimates is a function of different distributions of ages of entry in the sample as a whole and in the complier group (in which LATE is identified). If we are interested in estimating the effects of the policy expansion, our FE model provides a conservative estimate, as it in effect compares children who entered prior to age 1½ with some children who entered just a few months later (hence, having almost as long exposure to ECEC) as well as with children entering at a much later time (or not at all).

In contrast, the IV model may provide an estimate closer to the true effect of the policy expansion. If the policy expansion not only induced more children to attend at age 1½, but as part of this, induced slightly younger starting ages. This becomes clearest by considering the potential decision preferences, constraints, and opportunities among “would-be-compliers” (i.e., children in the “control” group for our IV estimates): children who were not in ECEC by age 1½ entirely due to the fact that policy had not sufficiently expanded in their municipality, but who would have enrolled by this time, if expansion had occurred. It is unclear why, for example, the lack of expansion among would-be-compliers would only affect selection preferences, constraints, and opportunities into ECEC at age 1½ but not in the following (or preceding) several months. While we do not have a means of investigating this empirically, if our speculation is correct, the average dosage differences between those in the “treatment” versus “control” groups would have been larger in the IV models than in the FE models. We also suspect that the estimate may be sensitive to the relation between the underlying ECEC exposure and the binary treatment (as is always the case when using dichotomization of continuous measures; DeCoster et al., 2009). We are not in a position to test this empirically, as our data only includes a binary indicator of ECEC use by age 1½, and not a continuous measure of age of entry into care, or total time of exposure.

A third reason may be bias in the FE models. Our sensitivity analyses indicate that these estimates are potentially sensitive to omitted variable bias. As mentioned, the sensitivity analyses are agnostic to the direction of the bias. We do not see an empirical route toward identifying what direction unobserved bias may be most likely to be influencing the coefficients. That is, we do not know whether (conditioned on our covariates) lower or higher achievers are more likely to select into (or out of) ECEC for unobserved reasons. On the one hand, under the strong assumption that potential unobserved bias is in the same direction as observed bias, our sensitivity analyses omitting observed covariates suggest that our FE models are positively biased. On the other hand, our IV models may offer a clue in the opposite direction. Our IV models, if valid, provide a more rigorous estimate of the causal impact of ECEC on achievement than do our FE models, one possible reason the FE estimates are smaller than the IV estimates is that our FE models are negatively biased by unobserved confounders.

Our findings must be considered in light of the content and context of the Norwegian educational system. In Norwegian ECEC centers, little attention is paid to direct teaching of academic content, and especially so during the earliest years. Because of the child-centered early childhood pedagogy, we suspect that the mechanism accounting for the treatment effect is that children who enter ECEC as toddlers gain the advantage in learning to learn, and in behavioral and effortful control, rather than learning specific school-related skills (Bailey et al., 2017). Almost all children attend their local neighborhood schools in a uniform school system with a national curriculum, without tracking or grade retention. Our inclusion of municipality and cohort fixed-effects reduces the risk that school choice or systematic between-school differences correlated with ECEC attendance rates bias our results. Yet, we are unable to determine whether the effect of ECEC is (exclusively) due to the pedagogical content. To the extent that increased ECEC use increases parents’ job opportunities, which may have an effect on child outcomes in the long run, this could potentially be part of the explanation.

Our results may have been influenced by spillover effects, which have been documented in targeted pre-K interventions (e.g., Williams, 2019). We are left to speculate whether this could reduce treatment effects because non-attenders should benefit from having a higher share of their classmates with ECEC experience. On the other hand, if teacher practices changed as a function of the share of children having ECEC experience by advancing more rapidly at school, this could potentially inflate the treatment effect, and again more so when a greater share of children are affected by the expansion. If either of these hypotheses are true, the consequence could be that the ECEC expansion influence children’s test scores via other channels than attending ECEC (i.e., peers). While we were not able to test whether this indeed is the case, we believe that this would not change the substantive value of our finding, because this would be part of the effect of the ECEC expansion.

How do our effect sizes compare to previous studies? As mentioned, we are not aware of directly comparable studies of school-age outcomes of universal ECEC for toddlers. From the literature on targeted preschool interventions, we know that immediate effects tend to decrease during the first few years in school (e.g., Barnett, 2011). With this in mind, the LATE estimates are in line with most other studies. With a similar design to ours, Felfe and Lalive (2018) found effect sizes of 20–30% of a standard deviation at age 6. In Norway, Dearing et al. (2018) found effect sizes as large as 89% of a standard deviation on language skills at age 3 for low-income children attending ECEC at age 1½. These positive effects are larger than those reported by Drange and Havnes (2019), who found effect sizes of about 15–25% of a standard deviation in first grade, as a function of starting ECEC at age 1 versus age 1½ for children of low educated parents in their lottery design. Both of these latter findings from Norway may underestimate the true effect, as their outcome measures were screening tests primarily designed for detecting low-performing children. In contrast, we use standardized national tests covering the full range of abilities. Nevertheless, the findings by Drange and Havnes (2019), with a very strong research design, underscore the potential value of attending ECEC early in the second year of life, consistent with our results. In sum, the idiosyncracies of studies with regard to context, design, age of testing, and type of outcome make direct comparisons of effect sizes impossible. Nevertheless, our findings are consistent with studies of ECEC programs for toddlers, finding positive effects particularly among children from families with low income or lower levels of parental education.

Somewhat surprisingly, we found the effects of ECEC to be more consistently differentiated as a function of parental education than family income, with the latter disappearing when both were included in the same models. Moderation of ECEC effects by education is in itself reported in several other studies (e.g., Drange & Havnes, 2019), while moderation by parental income was tested in other studies, for example by Dearing et al. (2018), using the same dataset as we did. This leads us, however, to speculate about the type of socioeconomic disadvantage for which the consequences are buffered by ECEC, as well as the sociopolitical context of this particular study.

Parental income and education are correlated, but to a varying degree across sociopolitical contexts. For example, the two are correlated about .70 in the US (Reardon, 2011), but only about .40 in Norwegian registry data. Parental income and education are supplementary indicators of SES (Duncan & Magnuson, 2003), and may affect the home learning environment for children differently (Duncan et al., 2015). Parental income through investment- and stress pathways (e.g., Longo et al., 2017; Yoshikawa et al., 2012), parental education through home learning environment, educational aspirations, and conversational styles (e.g., Magnuson, 2007). From our results, it seems to be the case that ECEC in Norway compensates for lack of opportunities stemming from lower parental education rather than income. This may be a function of a context of quite comprehensive support for families in Norway, including free health care, social safety net, and universal and subsidized ECEC. The exact processes for which ECEC compensates (at least in Norway) are yet to be determined.

Limitations

Despite several strengths, including large and nationwide survey data linked with administrative records on both parental income and education, and test scores, our study has limitations that must be taken into consideration. The first of these concerns external validity. MoBa includes a restricted sample, with underrepresentation of the least educated parents and those with the lowest incomes, as well as children with immigrant background. While the associations between the socioeconomic indicators and test scores are very similar among MoBa participants and the relevant population, we cannot rule out the possibility that there is a differential selection into MoBa of parents with children most likely to benefit from the expansion. If the parents with low levels of education or income participating in MoBa are, in some way, more resourceful and take better advantage of access to ECEC, this can be the case. Yet, our estimates may be a lower bound of the effect of the policy expansion if children of the least resourceful parents are, in fact, those who benefit the most from early ECEC attendance.

Moreover, our results are necessarily linked to a certain, and in one sense peculiar, context of a quite rapid expansion of ECEC for toddlers in a well-resourced and quite egalitarian country. There was a concern in Norway, at the time, that this expansion came at the expense of quality—that an increasingly larger number of toddlers put pressure on structural resources in the ECEC system, like teachers and space, ultimately resulting in lower process quality (Gulbrandsen & Eliassen, 2012). If this is the case, it may be reasonable to consider our effect sizes as a lower bound of potential effects, and that ECEC in Norway will have seen quality improvements as more teachers are trained, and the ECEC system consolidates to its increased coverage. We do, however, not have any evidence on whether this actually has happened. Moreover, we are unable to address heterogeneity in effects as a function of variability in structural- or process ECEC quality. This would potentially have added nuance to our findings.

As discussed above, our analyses are limited by only having a binary indicator of ECEC use at age 1½. If we had available exact starting age, we would be positioned to make stronger claims about the counterfactual conditions.

Implications

In this study, we demonstrate that universal ECEC starting in toddlerhood can contribute to closing socioeconomic inequalities in achievement in 5th grade. The practical implications for policy depend strongly on which of the two modeling approaches is given emphasis: which estimate is most policy-relevant? One might argue that the FE models inclusion of the full sample, regardless of why children were or were not in ECEC by age 1½, increases their generalizability. However, the policy significance of the IV estimates for compliers is underscored by the fact that ECEC expansion had such a large effect on ECEC attendance. Given almost equal response across socioeconomic groups documented in our complier analyses, the IV estimates apply to a large segment of children from families with low education and low income. This fact, combined with their internal validity advantages, leads us to believe that the IV estimates provide our most policy-relevant results.

For countries considering expansion (or implementation) of universal ECEC for toddlers, like the US, our LATE estimates are the most direct test of the effects which can be hoped for. If ECEC treatment effects are heterogeneous, which all of our results suggest, then such expansion may substantially reduce inequalities in achievement for those induced into ECEC by the expansion. We estimated that, conditional on covariates, the inequality in 5th-grade achievement between children of parents with 9 and 18+ years of education to be reduced by about 50% of a standard deviation, or well more than a year of learning. This reduction is considerable. In contexts where the most informative effect size is the comparison of children attending and not attending ECEC as toddlers (i.e., our ATE estimates), we found a reduction in these inequalities by about 10% of a standard deviation (or about a third of a year worth of learning), which is still important yet perhaps less spectacular. While the effect size most informative for policy may depend on the context, our findings support universal ECEC from an early age as a means to ensure that children from different socioeconomic background have more equal opportunities.

Open Research Statements

Study and Analysis Plan Registration

There is no study and analysis plan registration associated with this manuscript.

Data, Code, and Materials Transparency

The code underyling the results of this study (https://osf.io/bxe68) and the process for accessing the data underyling the results (https://osf.io/6jwak) are openly available on the Open Science Framework.

Design and Analysis Reporting Guidelines

There is not a completed reporting guideline checklist included as a supplementary file for this manuscript.

Transparency Declaration

The lead author (the manuscript’s guarantor) affirms that the manuscript is an honest, accurate, and transparent account of the study being reported; that no important aspects of the study have been omitted; and that any discrepancies from the study as planned (and, if relevant, registered) have been explained.

Replication Statement

This manuscript reports an original study.

Open Scholarship

This article has earned the Center for Open Science badge for Open Materials through Open Practices Disclosure. The materials are openly accessible at https://osf.io/qamkx/.

Acknowledgment

We are grateful to all the participating families in Norway who take part in this ongoing cohort study.

Additional information

Funding

The preparation of this manuscript was supported by funding from the European Research Council Consolidator Grant ERC-CoG-2018 EQOP [grant number 818425], given to the first author. The article is part of CREATE – Center for Research on Equality in Education, funded by the Research Council of Norway [grant number 331640]. The Norwegian Mother, Father, and Child Cohort Study is supported by the Norwegian Ministry of Health and Care Services and the Ministry of Education and Research.