---
title: 'Can information and assistance increase application and access to formal childcare:
  Experimental evidence from France'
author:
- "Laudine Carbuccia^[CRIS/LIEPP - Sciences Po & ENS PSL]"
- "Carlo Barone^[CRIS/LIEPP - Sciences Po]"
- "Coralie Chevallier^[ENS PSL]"
- "Arthur Heim^[Paris school of Economics & Cnaf]"
date: "`r format(Sys.time(), '%d %B, %Y')`"
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lang: en
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bibliography: ../PreReg_BIB.bib
abstract: "This trial assesses the impact of an intervention aimed at improving demand
  for and access to early childcare services (ECS) in France. The literature reports
  that attendance of high-quality ECS has positive effects both on women’s employment
  and on children’s development and school achievement, more so for children of low
  socioeconomic status (SES) families. However, these children are strongly underrepresented
  in ECS, especially in France. We hypothesize that structural barriers relating to the accessibility of
  ECS (rationing of places and criteria of access) and to their costs for the families
  only partly explain the lower demand for and access of low-SES families. Relying
  on a qualitative preparatory study in France, we expect that a lack of information about these
  services as well as behavioral and administrative barriers in the application process
  contribute to unequal access. Therefore, we designed an intervention targeting pregnant
  mothers and delivering information and support about the availability, costs, eligibility
  criteria of ECS and the related application procedures. We contact mothers during
  their visits to maternity wards of hospitals in the metropolitan area of Paris (Ile
  de France) and administer a baseline questionnaire to collect information on socio-demographic
  characteristics, knowledge of ECS, and intentions to use them. After this interview,
  they are randomly assigned to three experimental arms (control, information-only
  treatment, information plus administrative support treatment). One year later we
   administer a phone interview on actual recourse and two years later a follow-up"
always_allow_html: yes
subtitle: "A pre-registration report "
editor_options:
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```{=html}
<style>
body {
text-align: justify}
</style>
```

```{r loadlib,include=FALSE}
rm(list=ls())
list.of.packages <- c("knitr","tidyverse","readr","readxl",
                      'data.table','haven','randomizr',"DeclareDesign",
                      "MASS","modelsummary","lubridate","hdm",
                      "viridis","RColorBrewer","ggplot2","ggExtra","ggthemes","flextable",
                      "latex2exp", "sampleSelection", "marginaleffects",
                      "gmapsdistance","geosphere",
                      "googleway","maps", "mapdata","sp","ggmap")
#"stargazer","AER","latex2exp","readr","viridis","RColorBrewer","readxl", 'kableExtra','formattable',"ggplot2","ggExtra","ggthemes",'estimatr','SuperLearner','xgboost','foreach','doParallel', 'parallel','data.table','haven','randomizr',"DeclareDesign","MASS","modelsummary","lubridate","hdm","texreg","plm","ggdag","rsample",
#                      'glmnet', 'randomForest',"grf","DiagrammeR","ri2","ggeffects","modelsummary"
#)

new.packages <- list.of.packages[!(list.of.packages %in% installed.packages()[,"Package"])]
if(length(new.packages)) install.packages(new.packages, repos = "http://cran.us.r-project.org")
# 
invisible(lapply(list.of.packages, library, character.only = TRUE))

select <- dplyr::select
summarize <- dplyr::summarize

# I choose to use colorblind friendly colors
# The palette with grey:
cbPalette <- c("#999999", "#E69F00", "#56B4E9", "#009E73", "#F0E442", "#0072B2", "#D55E00", "#CC79A7")

# The palette with black:
cbbPalette <- c("#000000", "#E69F00", "#56B4E9", "#009E73", "#F0E442", "#0072B2", "#D55E00", "#CC79A7")

#GGplot default them : black and white.
    theme_set(theme_bw())

```



\newpage

# Introduction 

Early childcare services (ECS) play a critical role in shaping the lives of children and parents. First, they can increase labour market participation of mothers [@Kimmel1998;@NollenbergerRodriguez-Planas2015b; @Morrissey2017;@SimintziEtAl2022;@HermesEtAl2022; @HuberRolvering2023]. Second, high-quality early childhood interventions foster cognitive and socio-emotional development, improving educational attainment, and generate long-term positive outcomes in various dimensions [@CaseEtAl2005; @CunhaEtAl2006a;@CamilliEtAl2010;@Burger2010; @NoresBarnett2010; @JohnsonSchoeni2011;  @Barnett2011; @Attanasio2015; @Walters2015; @ElangoEtAl2016; @Kholoptseva2016]. 

Recently, @vanHuizenPlantenga2018 systematically synthesized quasi-experimental literature assessing the effects of access to childcare services between 2005 and 2017 across developed countries, analyzing 250 estimates derived from 30 studies that encompass a range of child development outcomes. These outcomes span from cognitive and noncognitive development during early childhood to educational achievement and adult income. This meta-analysis presents important results for childcare policy design. In particular, entry age does not seem to significantly influence outcomes, whereas the intensity of care play a role in certain cases. Childcare services offered through public provision have more pronounced effects on child development than private services. However, the most noteworthy finding is that the positive effects are primarily concentrated among children from socioeconomically disadvantaged backgrounds.

If policymakers want early childcare education to act as a means of reducing inequalities, they must ensure that those with the highest potential benefits can easily access it. Unlike the growing body of research highlighting the advantages of early childhood interventions, the assessment of universal childcare policies doesn't always yield the anticipated outcomes [@Cantillon2011; @GhyselsVanLancker2011; @VandenbrouckeVleminckx2011; @DuncanEtAl2012]. In most OECD countries, there is an socio-economic gap in early childcare enrollment, meaning that low-socioeconomic status (SES) parents access these structures the least [@OECD2016]. 

In this research, we investigate the barriers to formal childcare through a multi-arm experiment testing two easily reproducible policies.  In one treatment arm, the policy consists in providing information to parents through simple text-messages emphasizing important features of formal childcare and  links to more detailed information. In the second treatment arm, we also offer administrative support to register to formal childcare. 

France has a dual system where ECS is separated from preschool before entering elementary school. ECS are accessible to children as early as three months old, and preschool education is mandatory by the age of three. France has a relatively high coverage rate in ECS compared to other OECD countries, but this access is also one of the most unequal according to socio-economic background of families [@OECD2016; @CarbucciaEtAl2020]. The french ECS landscape is complex, with a mix of public, private, and associative providers, and a variety of ECS types. The most available type of ECS is private childminders, that account for 55.3% of ECS places in 2019 [@ONAPE2020]. Private childminders are also more expensive than public and associative daycare for low-SES parents. Public daycare applications are most often centralized at the level of the municipality or the district, while there is no centralization of applications for private or associative structures. Parents have to do one application per center for the latter. In a context of limited availability, parents should apply as early as possible during pregnancy and to as much ECS as possible since structures often have long waiting lists. Furthermore, the allocation of places in daycare centers follows a precise calendar that aligns with the school year. Since daycare centers operate on the school model with groups by age and because maternity leaves end two months and a half after birth, most places are allocated around June for households with a baby under one year old to start care in September. It is much less likely to obtain a place for a child over one year old.


This paper is a detailed pre-analysis plan of the effect of these interventions. It supplement the description provided with the pre-registration of the intervention and main outcomes on the AEA social science registry^[RCT ID AEARCTR-0009901] ([www.socialscienceregistry.org/trials/9901](https://www.socialscienceregistry.org/trials/9901))). This experiment has been approved by the IRB of Paris School of Economics^[IRB Number: 2022-015].

We formally explain under which conditions our design allows to measure each treatment's causal effects and better understand what factor affects decisions making and access to formal childcare. Ultimately, our main objective is to test interventions to  influence the demand size and structure, measure their effects on parents' search and application choices and behaviours, use of formal childcare, and uncover some plausible causal mechanisms. 




After presenting our motivations and details of the interventions in section \ref{sec:motivations},
we define and discuss our main research questions in section \ref{sec:question} and propose a theory of change in section \ref{sec:theoryChange} to guide our modelling assumptions, statistical analysis and interpretations. In section \ref{sec:models}, we formalize our target parameters, identification strategy and econometrics models. In section  \ref{sec:data}, we define the outcomes and measurement and finally, we pre-define our choices on the statistical analysis in section \ref{sec:stat}.





# Motivations context and intervention
\label{sec:motivations}


\subsection{Motivations: Early childhood intervention and social inequalities}
\sectionmark{Motivations}

Affordability and Accessibility are important supply side factors that can block access to early childcare. On the one hand, the costs of ECS can be too high for low-SES families. On the other hand, other factors may prevent families from accessing ECS, even when parents could afford it. For instance, access to public daycares is heavily rationed and governments are funding more and more facilities.
However, increasing supply for one type of childcare can have undesirable consequences. 
In France, @Pora2020 uses large but staggered increases in daycare provision across municipalities and time to estimate the effect of these apparent supply shocks on mothers’ labour market participation. On average, he finds no effect on labour market participation  but documents a crowding-out effect on registered childminders. These results have two implications. First, the childcare market offers different services in different segments, and the demand can shift from one segment to another. Second, the absence of an average effect does not mean that childcare has no effect on women’s participation in the labour market. If working gives higher priority in daycare assignment mechanisms, then there is no room for an effect on mothers’ labour market participation, at least at the extensive margin. Instead, these results suggest a general equilibrium effect in which women attached to the labour market shifts from childminders to daycare and manage to secure access for their children. In France, daycare centers have an objective comparative advantage in that they are, in general, the most affordable ECS solution. They also have a shared perceived comparative advantage over children socialisation, and researchers have documented that parents prefer collective childcare to childminders [@BouteillecEtAl2014;@CartierEtAl2017 ;@CaenenVirot2023]. 
Those who do not work (yet) are less likely to need childminders, and a lower demand brings a new equilibrium with a lower supply.

Surprisingly, this simple supply/demand/equilibrium reasoning is very much overlooked. However, it provides clear guidance on how policymakers may improve welfare and where interventions are likely to make things worse. Economics 101 tells us that going against market forces is not easy, and usually backfires. At the same time, letting markets free when there are strong externalities usually lead to welfare loss.  In the childcare market, tax subsidies and transfers already introduce distortions and may not be incentive-compatibles [@LanckerGhysels2012]. Especially when for-profit companies provide such services [@Penn2007; @NoaillyVisser2009].
There may also be *optimisation frictions* because information is not easily accessible, application process and tax-subsidies scheems are complex and so on. Because of heterogeneity in the effects of childcare on different populations, "who gets what and why" matters [@Roth2015]. The *quality* of the matching matters. Markets may be noxious because some participants are more vulnerable than others [@Satz2010g]. However, various interventions can lead to alternative potentially welfare-improving equilibria. One can even design better marketplaces. The recent work by @CombeHeim2023 models daycare assignment committees as matching markets. Their work shows that policymakers must *define* and *choose* how they consider the problem (with or without days), how they partition the supply across daycares (over weekdays) for different groups of children, and which definition of *fairness* they want to follow. A *fair* assignment is defined over a strict respect of priority rules or versions that tolerate some harmless deviations to increase the number of children assigned. They emphasize the trade-offs between different political objectives and the implication of each choice. *Fair* assignments ensure a form of *procedural justice* [@BinnsEtAl2018] and allow *transparency* as every decision can be justified individually.
Then, they show that there exist an assignment mechanism for each version of the problem that returns
the most preferred assignment by all families that respects the definition of fairness, multidimensional constraints and diversity quotas. Well defined priority criteria and diversity constraints offer powerful tools to enforce objectives over the distribution of assignments. However, as @Li2017 points out, \emph{"Market design have consequences. A consequence is richer than an outcome, it's the effect of the market on the world"}. In particular, the current market structures partly determine the composition of the demand. The lack of transparency and administrative burden may deter some families from even trying to register.


Behavioral sciences 101 suggest that market complexity inversely affects access to Early Childhood Services (ECS) for low-SES populations (see @CarbucciaEtAl2023 for an extensive review). Low-SES parents face difficulties on the demand side [@PavoliniVanLancker2018a], making it less likely for them to secure ECS placements. Several reasons contribute to this phenomenon.

First, low-SES families tend to exhibit a lower intention to apply for ECS for various reasons. Limited peer networks in the use of formal childcare lead to incomplete information about ECS during their decision-making [@CarbucciaEtAl2023 ; @Lazzari2012; @VandenbroeckLazzari2014], causing misperceptions about supply, such as overestimating costs and underestimating eligibility [@Carbuccia2023].

Second, decision-making factors exacerbate the information deficit. Parents, in part, rely on fast and frugal heuristics for childcare decisions, and the heuristic of adhering to social norms yields different outcomes based on social class [@ChaudryEtAl2010; @SandstromChaudry2012]. In low-SES communities, where ECS usage is less common, following social norms often results in not using ECS [@AbrassartBonoli2015a]. Conversely, this is the opposite for high-SES populations where using ECS is the norm.

Additionally, as the opportunity cost of staying at home and the career impact is lower for low-SES individuals, they are more likely to stick to the default situation of self-caring for their child. Lastly, ECS entails a cost in the present for uncertain future benefits, especially for those not currently employed. Low-SES populations have been shown to be  more present-biased and risk-averse, and tend to be more hesitant in such situations [@TverskyKahneman1974 ;@PepperNettle2017].


<!-- Behavioral sciences 101 predicts that the more complex the market is, the lower the access to ECS for low-SES -->
<!-- populations (see @CarbucciaEtAl2023 for a complete review of why it is the case). Indeed, on the demand side, low-SES parents are less likely to overcome the difficulties created by the market in accessing a place. On the one hand, low-SES families may first have a lower rate of intention to apply for several reasons. First, low-SES parents are more likely to have incomplete information about ECS when doing their childcare decision-making due to limited peer networks using formal childcare @CarbucciaEtAl2023 @Lazzari2012 @VandenbroeckLazzari2014. These parents may thus have more misperceptions about the supply, such overestimating the costs and underestimating their eligibility @Carbuccia2023. Second, information factors may be reinforced by decision-making factors. To the extent that parents rely at least partly on fast and frugal heuristics for their childcare decisions-making, the heuristic of following the social norm would lead to different output according to the social class @ChaudryEtAl2010. In low-SES communities where fewer people use ECS, following the social norm would most often lead to not using ECS, while the opposite is true for high-SES populations since most of their peers use ECS. Besides, because the opportunity cost of staying at home and the impact on career are lower for low-SES population and their baseline employment rate is lower, low-SES parents would also be less likely to stick to the default situation that is caring of the child themselves. Finally, while using ECS means paying a cost in the present for temporally distant and uncertain benefits - especially if one is not employed yet -, low-SES populations are known to be more present-biased and risk-averse @Kahneman2013 @PepperNettle2017.  -->

On the other hand, even when low-SES parents do intend to apply for a place at a ECS, they may also face more behavioral barriers in their application process. First, because low-SES parents are less familiar with administrative procedures and vocabulary, they may face higher friction costs when applying and therefore be less likely to complete the application process [@Sunstein2022]. Secondly, because their cognitive resources may be more focused on more pressing issues during pregnancy and the early years (e.g. paying bills, housing) and they are less informed about the tips and tricks, they may apply less efficiently, i.e. *later* and to fewer structures, which is detrimental in the context of low-supply. Since low-SES parents are also less likely to benefit from influential social resources, the more complex and obscure the system is, the higher the barriers for low-SES populations. In this context, helping low-SES parents navigate the system by delivering essential information and by directing help in the application process should reduce at least the SES gap in ECS application, if not in ECS enrollment.



<!-- 
Behavioral sciences 101 predicts that complex markets structures likely prevent access to low-SES populations. Indeed, they create more room for information and behavioral assymetry according to socio-economic status.   They may lack information due to limited peer networks using formal childcare \todo{Arthur on garde ces deux dernières phrases ?}. 
Unrealistic cost estimates, acceptance chances, and a lack of awareness about childcare options can deter them Low-SES communities, where fewer use ECS, may also conform to this social norm, leading to fewer ECS applications. Additionally, low-SES families may face behavioral barriers during the application process due to administrative unfamiliarity and cognitive resource constraints. To bridge this gap, delivering essential information and reducing application friction costs can help low-SES parents access ECS, potentially mitigating SES disparities in ECS application and enrollment.
There are many potential reasons for that. For instance, low-SES parents less likely to use formal childcare so there are less peers to seek information from. People may have unrealistic estimates of costs, their chances of being accepted, the application process and so on. More generally, they may not know precisely what childcare exist or these options may be less salient. Second, to the extent that parents rely at least in part on fast and frugal heuristics to make their childcare decisions (including the starting point of whether or not they want to use ECS), following the social norm leads to different outcomes in different groups. In low-SES communities where fewer people use ECS, following the social norm most leads to not using ECS, while the opposite is true for high-SES populations in which most people use ECS. Given that the opportunity cost of staying at home and the career impact are lower for low SES populations, and that their basic employment rate is lower, they would also be less likely to stick to the default situation of caring for the child themselves. Besides, using ECS means paying a cost in the present for temporally distant and uncertain benefits - especially if one is not employed yet -, while low-SES populations are known to be more present-biased and risk-averse. For all these reasons, low-SES families may be less inclined to apply in the first place. Besides, even when low-SES parents do intend to apply for a place at a ECS, they may also face more behavioral barriers in their application process, leading them to access ECS less in the end. Firstly, because low-SES parents are less familiar with administrative procedures and vocabulary, they may face higher friction costs when applying and therefore be less likely to complete the application process. Secondly, because their cognitive resources may be more focused on more pressing issues during pregnancy and the early years (e.g. paying bills, housing) and they are less informed about the tips and tricks, they may apply less efficiently, i.e. *later* and to fewer structures. Since low-SES parents are also less likely to benefit from influential social resources, the more complex and obscure the system is, the higher the barriers for low-SES populations. In this context, one direct implication of that is that helping low-SES parents navigate the system by delivering essential information to all parents by default, and diminishing the application friction costs by helping them with the application process should reduce at least the SES gap in ECS application, if not in ECS enrollment. -->


<!-- Understanding demand and implementing policies that foster access for those who are more likely to benefit from childcare and generate positive externalities is a promising intervention area.  -->

<!-- ## Context: Barrier to formal childcare in France -->
<!-- \sectionmark{Context} -->

<!-- From this discussion, it is clear that attributing the underrepresentation of low-SES families in the ECS solely to supply side factors paints an incomplete picture. In the public discourse, this underrepresentation is occasionally ascribed to a preference for informal childcare arrangements. Alternatively, we have shown in a previous systematic review and meta-analysis that informational and behavioral factors (e.g. underprivileged parents overestimate the costs of these facilities; they procrastinate the application) could also contribute to this access gap [@CarbucciaEtAl2023]. Subsequent qualitative fieldwork conducted in a French context reaffirmed these findings [@Carbuccia2023]. To the extent that they play a significant role in the SES gap in ECS access, these barriers could substantially limit the impact of structural reforms that target affordability and accessibility.  -->


<!-- We hypothesize that structural barriers relating to the accessibility of ECS (rationing of places and criteria of access) and to their costs for families only partly explain the lower demand for and access to low-SES families. Relying on a qualitative preparatory study, we expect that a lack of information about these services, as well as administrative and behavioral barriers in the application process, contribute to unequal access. Therefore, we designed an intervention targeting pregnant mothers and delivering information and support regarding the availability, costs, eligibility criteria for ECS, and related application procedures.  -->


<!-- Informational barriers and behavioral barriers require different levers of action: direct information to families in the case of the former, and assistance with procedures (e.g. forms filled in with families) for the latter. It therefore seems essential to be able to estimate the weight of behavioral versus informational barriers, since large-scale deployment of administrative support would be far more costly for local authorities. Knowing not only the various mechanisms  responsible for the observed differences in participation, but also the relative weight of each is therefore a priority, in order to best guide the implementation of appropriate public policies. There is no single study, either in France or internationally, that can be used to estimate the weight of the various dimensions involved. Besides, while the effects of childcare policy also vary across countries with different welfare states, across populations within a country with different social and gender norms [@Holloway1998; @VandenbroeckEtAl2008; @KahnGreenberg2010],  not much is known about the determinants of the SES gap in ECS enrollment in the French context.  -->


## The interventions: information and social support to foster access to formal childcare 

 \sectionmark{The interventions}
To address this gap in knowledge and address these inequalities, we conduct a randomized control trial in France with three arms: a control group and two treatment groups. The timeline of the experiment is presented in Figure \ref{fig:timeline}.
The first treatment group (T1) receives information about early childcare service options through an inexpensive and easily scalable design, while the second treatment group (T2) receives the same information, complemented by administrative support via phone calls. From a policy perspective, distinguishing between the effects of these two treatments is of paramount importance. T1 represents a cost-effective intervention that any policymaker would consider when confronted with the issue of the ECS access gap, which could be readily expanded if its effectiveness is demonstrated. However, given the potential presence of additional behavioral barriers preventing low-SES parents from taking action, even when they express an intention to use ECS, this treatment may yield minimal to negligible effects in closing the access gap, despite the reminders. This underscores the need to compare T1 with T2, a treatment designed to address in-depth behavioral barriers.


The aim of this study is, therefore, to evaluate the impact of these interventions on

(i) application behavior, 
(ii) access to an ECS slot.

Ultimately, follow-up surveys would allow us to provide causal evidence of the impact of access to ECS on 

(iii) mothers' labor market outcomes and 
(iv) children's development.

Between September and December 20233, we contacted pregnant mothers (4 to 9 months of pregnancy) during their visits to maternity wards of hospitals in the metropolitan area of Paris (Ile de France) and administered a baseline questionnaire to collect information on socio-demographic characteristics, knowledge of ECS, and intentions to use them. After this interview, they were randomly assigned to three experimental arms (control, information-only treatment, information plus administrative support treatment) within blocks of pre-registered covariates. One year later we administer a phone interview on ECS use and two years later a follow-up to measure long-term impacts on child development and labor market outcomes.

The treatment arms are as follows:

\begin{enumerate}
\item {\bf Information-only} (T1) (\emph{October-December 2022}): this involves two clusters of contents 
\begin{enumerate}
\item  \label{Cluster1} {\bf Cluster 1}: information aimed at helping families to identify a type of ECS that fits well with their preferences and constraints. Treated families receive a text message providing access to a short video presenting information on the availability and characteristics of different types of ECS in France and how they may correspond to the different preferences and needs of families. One text message reminder is sent to encourage mothers to watch this video. In the following days, a second text message with related reminders gives access to a second short video on eligibility to and costs of ECS in France and a third video presents detailed information on a specific type of childcare service (halte-garderies) which may be particularly well-suited to low-SES families (less intensive care, less restrictive criteria of access, easier application procedures and more flexible time schedules).  

\item  {\bf Cluster 2}: information aimed at understanding the application process. Like for \ref{Cluster1}, this involves sending text messages and related reminders with links to two videos presenting information on the calendar of applications, the procedures to apply, and tips to maximize the chances of success, such as applying to multiple ECS. The content of the first video of this cluster will vary depending on the district where families live, as each one has a specific application process. 

\item {\bf Reminders:} Reminders on Cluster 2 is sent by text messages after birth (February 2023) in order to maximize applications for the June commission, where most of the slots get allocated. We send also generic reminders to apply shortly before the deadline for the 2023 applications to ECS (April 2023).
\end{enumerate}

\item  {\bf Information then administrative support treatment} (T2) (\emph{February-April 2022}):
This involves one or several phone calls with parents to deliver personalized assistance, as well as personalized application reminders. 
We randomly assign the sample over groups of two weeks of intervention and research assistants. During this period, we call each parent as many time as needed to reach them. We present our services to parents according to a systematized procedure. When parents show interest, we first establish a diagnosis of their choices, intentions, and needs after birth. Parents are at very different stage of their decision making and we adapt our intervention accordingly.  
When they have not decided yet, we help them identify the ECS solution that best fits their needs, including how accessible each solution is given their situation, and how affordable each solution is through cost simulations. When they have identified the type of ECS they want, we assist them according to their demands. Some just need help to spot the ECS structures they could apply to, while others need us fill the application forms with them. We code each type of assistance in a systematic way to qualify the intensity of assistance provided, and create a typology of the types of situation parents were in.
Parents also receive the same information as T1 according to the same timeline. We call this treatment "administrative support".

\item { \bf Control group}
Parents assigned to the control group receive a \emph{placebo} treatment. We wanted to maintain some contact to minimize attrition at endline. Theses messages were also sent to the two intervention groups for the same reason. These text messages are about 
\begin{enumerate}
\item general events throughout the year (e.g., welcoming text message, winter and summer holidays, new year), and 
\item some useful tips not affecting our outcomes of interest (e.g., flea markets around Paris). Importantly, participants in the control group also receive videos, but not about ECS. The content of the videos are about emotions during pregnancy. 
\end{enumerate}
\end{enumerate}



Importantly, neither the information nor the administrative support interventions are prescriptive about childcare choices. Our goal is to help people be informed, make choices on their own with or without guidance and assistance with formal applications. 


```{=latex}
\begin{figure}[h!]
\caption{Timeline of the experiment}\label{fig:timeline}
%\resizebox {\textwidth} {!} {
  \begin{ganttchart}[
    %\small
    y unit title=.36cm,
    y unit chart=.28cm,
    % bar height = 0.4,               % <---
      vgrid,
    expand chart=\textwidth,
    time slot format=isodate-yearmonth,
    time slot unit=month,
    title/.append style={draw=none, fill=RoyalBlue!75!black},
    title label font=\tiny \sffamily \bfseries \color{white},
    %title label node/.append style={below=-1.6ex},
    title left shift=.05,
    title right shift=-.05,
    title height=1,
    group/.append style={draw=black, fill=RoyalBlue!75, font=\tiny},
    bar/.append style={draw=none, fill=RoyalBlue!50},
    bar height=.6,
    bar label font=\tiny \color{black!50},
    vrule label font=\tiny,         % <---
      title label font=\bf\tiny\color{white},         % <---
      bar label font=\tiny,           % <---
      group label font =\bf\small,
    group right shift=0,
    group top shift=.6,
    group height=.3,
    group peaks height=.2,
    bar incomplete/.append style={fill=Purple},
    milestone label font=\tiny
  ]{2022-08}{2025-03}
  \gantttitlecalendar{year} \\
  \ganttgroup{Recruitment and baseline}{2022-09}{2022-12} \\
  \ganttbar[bar/.append style={shape=rectangle, fill=CornflowerBlue!50, dashed}]{Randomization}{2022-10}{2022-12} \\ -->
  %\ganttbar[bar/.append style={shape=rectangle, %fill=CornflowerBlue!50, dashed}]{Baseline Survey }{2022-11}{2023-02} \\
\ganttbar[bar/.append style={shape=rectangle, fill=Purple, dashed}]{\bf{Information treatment (T1+T2)}}{2022-10}{2023-02} \\
\ganttbar[bar/.append style={shape=rectangle, fill=Purple, dashed}]{\bf{Administrative support (T2)}}{2023-03}{2023-06} \\
\ganttmilestone{\emph{Daycare assignment committees}}{2023-05}\\
\ganttgroup{Endline Survey }{2023-10}{2023-12} \\
\ganttgroup{Follow-Up Survey }{2025-01}{2025-03} \\

\end{ganttchart}
%}
\end{figure}
```


<!-- Sample size: 1849 families.  -->






# Research questions
\label{sec:question}

## Definitions 

We designed this intervention to answer the following research questions:
\begin{enumerate}
\item \label{RQ1} {\bf Can information and assistance increase applications and access to formal childcare?}
\begin{enumerate}
\item \label{RQ1a} \emph{Is this effect heterogeneous across socio-economic background ?}
\end{enumerate}
\item \label{RQ2} {\bf Does providing administrative support boost application and access compared to providing only information?}
\begin{enumerate}
\item \label{RQ2a} \emph{Is this effect heterogeneous across socio-economic background ?}
\end{enumerate}
\end{enumerate}

Consistent with the motivations presented in section \ref{sec:motivations} above, these research questions are policy oriented. Our primary objective is \ref{RQ1}:  to test if we can increase application and access to formal childcare using two easily reproducible interventions and \ref{RQ2}: measure how much active assistance for search and application increase access compared with no intervention or simply additional information.

## Implication for the analysis

Question \ref{RQ1} translates in an analysis of the average effect of our intensive treatment T2 on a measure of access to formal childcare. Question \ref{RQ1a} assesses overall treatment effect heterogeneity by socioeconomic background. It can be estimated by comparing pooled treatment effects between blocks of low and high SES. We used a block-randomization design to ensure balance between treatment arms for this purpose.

Question \ref{RQ2} relates to the treatment effect heterogeneity between treatment arms. With a three arms randomized control trial, there are several comparisons we can make. T2 is an "expensive", labor-intensive policy and T1 is a "low-cost" alternative. Therefore,

- Comparisons between T1 and control tests how "*unsolicited provision of information*" (as implemented) affects application behaviors and enrollment.

- Comparisons between T2 and T1 tests how, *after the provision of unsolicited information*, being *offered optional assistance and support* to apply for formal childcare affect outcomes.
- Comparing outcomes of T2 against control tests the overall effect of information and administrative support.

The last comparison captures the effect of both treatments and their interaction. We discuss it hereafter more precisely.

<!-- - Comparing gains between T2 and control and gains between T1 and control. Administrative support is meant to help people make choices, take actions accordingly, and ease the administrative burden. -->

Each choice regarding childcare is an important decision made under binding constraints. Informed decision making requires good knowledge of all options, benefits, costs, and also opportunity costs and benefits. The information treatment aims at helping parents defining their choice set and adjust their expectations. It makes potential benefits and costs (e.g., direct cost of a place, opportunity costs, flexibility) of using ECS clearer. It also make administrative burden more salient and potentially increase the need for help. However, some parents may not react to the information. After all, the information treatment are unsolicited which can be seen as a nuisance. They may not trust the source, or may simply missed our messages. 

<!-- In other words, there is an unobserved group of *information sensitive* parents which constitute a latent *information complier* group\todo{So do we talk about it or not ?}. These parents cannot be identified properly^[Some variables may proxy information sensitivity. For most parents, we know if they opened the link in the text-message. However, we don't know if they watched them entirely, partially or not at all.]. However, if there is an effect of T1, that is because this population exists and reacts to the information treatment.  -->


Those in T2 are offered an additional intermediary choice: receiving help. Receiving help is observed. We know who complies with assistance among those in T2. However, since they received information before this choice, the relevant counterfactual for T2 compliers can only be identified in comparison with the T1 sample. 
With random assignment within blocks, we can estimate the characteristics of those compliers based on comparisons of baseline observables with T1 [@Abadie2003; @AngristEtAl2023].  In particular, Question \ref{RQ2a} is tightly linked to compliance heterogeneity and the distribution of potential outcomes across high and low socio-economic background. All of which are identified using treatment assignment as instrument of receiving assistance among T2 and T1 as a control group. 
<!-- The comparison of T2 with control is more ambiguous because there may be defiers^[See the discussion in the identification strategy]. However, we can estimate the intention to treat effect of information, the intention to treat effect of information and administrative support and compliance with assistance among the informed. These results may be informative to identify or bound  relevant causal parameters [@BehaghelEtAl2013]. -->


However, our conclusions on questions \ref{RQ1}, \ref{RQ1a},  \ref{RQ2}, and \ref{RQ2a} cannot be solely based on the magnitude and significance of these treatment effects. There are many intermediary channels through which the interventions can increase access to childcare, or not. 
This research project also aim at understanding *how* and *why* we may observe some effects and when we may not.
We define a simple theory of change to guide the definition of additional research questions.  

# A theory of change and additional research questions
\label{sec:theoryChange}



```{r ThChange, results='asis', echo=FALSE, cache=TRUE, out.width='50%',fig.cap="Theory of change: illustration"}
path <- getwd()
#knitr::include_graphics(paste(path,'../Preregistration/Drafts/TOC/toc.JPG',sep='/'),error=FALSE)
knitr::include_graphics('../Preregistration/Drafts/TOC/toc.JPG',error=FALSE)

```


<!-- ![Theory of change](../Preregistration/Drafts/TOC/toc.JPG){width=50%} -->

Figure \ref{fig:ThChange} represent our simple theory of change. It focus on the paths through which the treatment effects are likely mediated. At every level, the comparison between different treatment arms provide informative metrics on causal mechanisms fostering or preventing access to formal childcare. We formally define the different set of outcomes as followed:

:::{.definition #Intermediary name="Intermediary outcomes"}
  The intermediary outcomes are parents level of information and perceptions of ECS. It should be noted that an increase in the level of information and/or a change in perceptions are not a necessary condition for the proximate outcomes to happen. Indeed, there is another, non measurable, channel that is behavioral barriers alleviation. Therefore, if we observe a change in our proximate outcomes but no change in our intermediate outcomes, it will indirectly imply that this change is a result of behavioral barriers alleviation only. 
:::


:::{.definition #Proximate name="Proximate outcomes"}
The proximate outcomes are parents' intention to apply to ECS and application behaviors as measured by their attempts to access ECS, the timing and number of applications.
:::


:::{.definition #Final name="Final outcomes"}
The final outcomes are divided into two sets:
\begin{enumerate}
\item {\bf short run:} access to ECS
\item {\bf long run:} children development and parents' labour market participation, incomes, family structure.
\end{enumerate}


:::



We wanted to make clear the nested relationships between different sets of outcomes. For our intervention to affect the final outcomes, it needs to change proximate outcomes. 
We think that this can only happen if there is an effect on intermediary outcomes.
<!-- as defined in our theory of change. If there are effects on proximate outcomes but not in our intermediary outcomes, either our measurement is not capturing  \todo{Je suis pas sure de comprendre pourquoi on devrait conclure que c'est innaproprié ?} or the information treatment triggers other behavioral changes (e.g. a reminder effects rather than a information effect). -->
Furthermore, if there are important treatment effects on proximate outcomes but no final outcomes, it shows evidence of rationing and mismatch on the childcare market.
In other words, we use a deductive approach to understand causal mechanisms with pre-specified interpretations of our econometric analysis.

Additionally, we link question \ref{RQ1} to wider *consequences* which we include as *long run final outcomes*. We think of these consequences as reduced-form measures of the shock created by our intervention which *potentially* jointly affected parents decision in many dimensions and through different channels. The main difference between the long term outcomes and the others is that we do not have all the relevant information to interpret the results.  However, we expect the results on the other set of outcomes to be informative and guide a more formal set of hypotheses. Therefore, these analyses will be conducted in another study with a dedicated pre-analysis plan.


<!-- \todo[inline]{J'ai écrit ça après mais je me rend compte que ce serait mieux de pré-register ici que les trucs sur le survey et dire que les "administrative data will be analysed in another paper and we will register a specific PAP once we know which database and which variables will be available". tu crois pas ?} -->

<!-- \todo[inline]{Laudine: siiiiii} -->

<!-- Formal childcare is accessed through a market, and we expect our interventions to change the composition and size of the demand [@HermesEtAl2022]. Successfully securing a slot depend on institutional settings, priorities in daycare assignment mechanisms,  congestion, access to alternative options and so on [@CombeHeim2023]. -->
<!-- Formal childcare affects the allocation of time for parents and may induce adjustments on the labour market and disposable income [@KalenkoskiEtAl2005; @KendigBianchi2008]. Each parent, each family face a form of constraint optimisation problem where they have to balance (potential) additional labour incomes with childcare costs and against the opportunity cost of parental and informal care, the expected benefits or drawbacks of childcare on their children, and so on [@SandstromChaudry2012;@GousseEtAl2017; @ZanggerWidmer2020;@GuptaEtAl2023]. The resulting equilibrium depend on beliefs and norms [@GongEtAl2022], especially gender roles and *performative motherhood and fatherhood*  [@Holloway1998 ;@Nentwich2008a ;@Bauer2016;@Valiquette-TessierEtAl2019; @HanEtAl2023; @Reich-StiebertEtAl2023],  linked to stress, fatigue and parenting behaviours [@SchullerSteinberg2022], couple stability and so on [@BriselliGonzalez2023;@CurranEtAl2021; @Jessen2022b]. Labour market effects also depends on job opportunity and market tightness, travel distance and institutions such as flexible hours [@FlecheEtAl2020;@LeBarbanchonEtAl2020; @Chung2020]. -->
<!-- Therefore the analysis of  consequences will be exploratory and related to our intermediary results. -->

<!-- \todo[inline]{Laudine: je trouve ce paragraphe TROP stylé, mais je suis pas sure qu'il soit bien placé -->
<!-- Arthur: d'où ma remarque precedente -->
<!-- } -->


We now move to the formal definitions of our empirical strategy.




# Research strategy

\label{sec:models}

We start by briefly describing the data source, timing and their main contents. 
Then, we define the notations to define models and our identification and estimation strategies. We discuss inference together with the presentation of the models.

## Data sources

### Baseline and endline survey

The experimental design embeds a baseline survey which generates an initial database containing a set of parents fitting our inclusion criteria and constitute the experimental sample. Undocumented migrants were excluded. We also excluded participants under 18, participants that do not have a cell phone or did not agree to leave their phone number, and participants living outside of our targeted areas (Paris, Seine Saint Denis, and Val de Marne) or about to move out of these regions.
The experimental sample was then randomly split into the three treatment arms shortly after recruitment. We answer our main empirical questions for this analysis from surveys:

-  **baseline** (September - December 2022) 
- **endline survey** (October - December 2023) 

Both are collected through computer assisted interviews by the research team with trained research assistants (in-person interviews for the baseline and CATI for the endline). All questionnaires contain information about parents' socio-demographic characteristics, intended ECS use (or actual use for Endline), ideal childcare arrangements (type, intensity), perception of the supply (monetary and non-monetary costs of using childcare vs. staying at home, accessibility), perceived social norms and beliefs about children's development during the early years. Importantly, both questionnaires also cover additional set of outcomes (e.g., mental well-being, breastfeeding, smoking) so that the participants remain unaware of the goal of study.

If we manage to secure additional funding, we also plan an follow-up survey one to one and a half years after the endline survey and matching with administrative records from the National family allowance fund (Cnaf) and employment records. These analysis will have their own pre-analysis plan.

We present the details of each survey in section \ref{sec:data}.

### Power analyses and sample size determination
See the "sample size" section within the "Experimental design" section of the main information for registration document. 
 
 



<!-- - **Administrative data**: data on the coverage rate in ECS from the Caisse nationale des allocations familiales (Cnaf, National Family Allowance Funds) at the city level, data from the Cnaf on family characteristics and related childcare benefits use, data on labor and training participation, especially the FORCE database  (Formation, Welfare, and Employment), and results of the national students' assessments of first, second, and sixth-grade students. -->

## Notations


 

\subsubsection{Samples and observables}

At baseline, we observe a sample of $N_b$ pregnant mothers we call *individuals* indexed $i \in \{1:N_b\}$. This sample has a nested structure by maternity ward and lottery. Individuals $i$ recruited in a given ward and subject to a given lottery belong to a *wave*  $w \in \{1:W\}$ ^[There were 7 waves. Every two weeks, we proceed to random assignment.]. We note $W_i$ the wave of individual $i$. We collect a lot of information on each mothers, some of which have a specific role in our research strategy.


First, we define blocks of individuals based on the cross product of three variables:

- **Education** $E$ ("tertiary"/"secondary or lower") 
- **Intention to use ECS** $I$ ("no"/"yes but never has"/"yes and already has")
- **Supply** $S$ ECS coverage rate higher/lower than the average in the department.

Let $b_i \in \{1:B\}$ denotes the block of individual $i$ defined as the product set of the blocking variables and waves $(E_i,I_i,S_i,W_i)$. 
Let $B_i=\one{b_i=b}$ denotes block-dummies and $\mathbf{B}$ the matrix of blocks. 

Block-randomization serves two purposes. 

1) We want to reduce noise in our estimations and 
2) be able to compare treatment effects across subgroups.

Our choice is guided by the discussion in section \ref{sec:motivations} which gives a simple rationale: parents' level of education is strongly associated with childcare use, parents who intend to use ECS are more likely to apply, but this may be more or less effective depending of the ECS coverage rate. Education is linked to intention to use and parents strategy may be different by education groups if supply is high or low.
Therefore accounting for these interacted characteristics is expected to reduce the residual variance thus, improving precision of our treatment effect estimators. 
Since one of our main research questions is about treatment effect heterogeneity between high and low SES, blocking also ensures balance between groups and independence between education and treatment.
Furthermore, treatment effect heterogeneity across different sets of blocks can be informative about mechanisms. 
<!-- Last, intention to use also has an additional special role in the interpretation of our results. We discuss that after introducing all notations. -->


All variables measured at baseline constitute a set of attributes bundled in a matrix $\mathbf{A}$ of size $(N_b,A)$.  Attributes may vary with time but their measurement at baseline are informative of the parents situation at that time. This matrix includes $E_i$, $I_i$, $S_i$, $W_i$ and $B_i$ and other variables, among which we select $\mathbf{X} \subset \mathbf{A}$, a set of relevant attributes for each analysis. The method for choosing variables in $\mathbf{X}$ depend on the problem. 
We observe individuals $i$ again in the endline survey with $N_p \leq B_b$ observations. 
Note that the difference between the two sample size must be investigated and may require statistical adjustment in case of differential attrition (See section \ref{sec:attrition} below).

This survey generates the set of outcome variables. In our general presentation, we follow the usual conventions and denote an outcome as a random variable $Y$. $Y$ follows different definitions across sets of outcomes (intermediary, proximate and final) and  which measurement of the outcome is used. We only assume that all distributions have finite first moments and that each observation $Y_i$ is a realization of the random variable $Y$ drawn from the same data generating process. We denote $\mathbf{Y}$ the matrix of outcomes. 
Some outcomes variables are related and we denote $\mathbf{Y}^f\subset \mathbf{Y}$ for a *family* of outcomes.
We abuse of notations and also denote $\mathcal{H}^f \in \mathcal{H}$ a family of hypotheses with associated statistical tests to define the sets over which we adjust the Family-wise error rate.

\paragraph{Notations for the main families of outcomes}


The family of intermediary outcomes is noted $\tilde{I}\subset \mathbf{Y}$ and contain variables that captures the levels of information, perception of ECS and so on. The family of proximate outcomes measure application behavior.
We let $\mathbf{\tilde{D}}\subset \mathbf{Y}$ be the matrix of measurements of application behavior. 
Finally, we let $\mathbf{\tilde{Y}}\subset \mathbf{Y}$ be the matrix of measurements of final outcomes.


<!-- The simplest measurement is a dichotomous variable that equals 1 when parents report applications for formal childcare made on their own. We also have questions as to which childcare arrangement they applied and measures of the number of applications. -->


<!-- There are other observables $\mathbf{O}$ measured in this survey which can be used as outcomes or compared with baseline values. -->


\subsubsection{Treatment variable and potential outcomes} We denote $Z^g$ the random variable that maps treatment assignment status such that:
$$
g=\left\{
\begin{aligned}
2 ~&:=\text{({\bf T2}): } Offered assistance\\
1 ~&:=\text{({\bf T1+T2}): } Offered information\\
0 ~&:=\text{({\bf T0}): } Offered placebo
\end{aligned}
\right.
$$

and $Z_i^g=\one{g_i=g}, g  \in \{0,1,2\}$ denote treatment offered to individual $i$. These variables do not define treatment arms but which intervention they receive. Therefore, those in T2 have both $Z_i^2=Z_i^1=1$.

We also note $\bar{Z}^g=\one{g_i\neq g}$ to note groups who did *not* receive treatment $g$ and conveniently restrict subsamples using this notation.

\paragraph{Potential outcomes with information treatment}

Following @Rubin1974 causal model based on potential outcomes, we assume that treatment assignment reveal potential outcomes and SUTVA (*stable unit treatment value assumption*).  

Let $Y_i(1)$ and $Y_i(0)$ denote potential outcomes when parents received information or not respectively. Note that these potential outcomes are defined as *intention to treat* parameters. $Y_i(1)-Y_i(0)$ is the individual gain of having access to our information treatment.
<!-- We do not know the *information complier* type. -->

Among T1 and T0, treatment status link observed outcome $Y_i$ with potential outcomes through this switching equation :
\begin{equation}
Y_i=Z_i^1Y_i(1)+(1-Z^1_i)Y_i(0)\quad \forall i s.t. \bar{Z}^2_i=1
\end{equation}

In words, we assume that observed outcomes in randomly assigned treatment arms reveal potential outcomes. 
Let $Y_i(2)$ denote potential outcomes when parents **received assistance**. It depends on parents choice to accept help. 

## Experimental design and identification

\subsubsection{Assumptions}

We explicitly define the standard assumptions that our setting is meant to satisfy by design [@AtheyImbens2017a].
Treatment status $Z_i$ was assigned using block randomisation and therefore implies:

:::{.hypothesis #indep name="Independance by block randomisation"} 
\begin{equation}
 \big(Y_i(0),Y_i(1),Y_i(2),\mathbf{X}_i,D_i(1),D_i(2)\big)\perp Z_i |B_i
\end{equation}
:::

Assuming our randomization went well, this assumption is verified which is sufficient for a causal interpretation of all intention to treat parameters (see below). It also gives a causal interpretation to the *first stage* effect on support take-up. 
<!-- Because we randomized within blocks, we can estimate heterogeneous treatment effects for subgroups based on those characteristics by computing weighted average of within-block treatment effects over the relevant set of blocks weighted by the relative size of each block.  -->

<!-- To identify the effect on assistance compliers using instrumental variables [@AngristEtAl1996; @Abadie2003],  -->
<!-- let us further explore the case of compliance with T2. -->



\paragraph{Compliance with support}


Let $D_i=\one{accept assistance}$ denote the parsimonious binary variable coding for receiving our support. By design, $D_i=0 \forall i s.t. \bar{Z}^2_i=1$ ; nobody in T1 or T0 could access our support. Those with $D_i=1$ are those in T2 who accepted our support, but only after receiving information, like T1.

$D$ measures who accept help to navigate administrative burden of ECS enrollment after receiving low-cost information. This compliance rate is a policy relevant parameter for our experiment. It captures the  *demand for help* (when offered, and among those informed).

In the instrumental variable framework, Participation $D_i$ is also the realization of potential participation revealed by random assignment. Let $D_i(0)$ $D_i(1)$, $D_i(2)$ denote potential participation *switched* by $Z_i^1$ and $Z^2_i$ by the following equation:

\begin{equation}
\label{POD}
D_i=\underbrace{D_i(0)+Z_i^1\big(D_i(1)-D_i(0)\big)}_{=0}+Z^1_iZ_i^2\big(D_i(2)-D_i(1)-D_i(0)\big)
\end{equation}

- When $Z_i^1=Z_i^2=0$, $D_i=D_i(0)$. 
- When $Z_i^1=1$ and $Z_i^2=0$, $D_i=D_i(1)$
- When $Z_i^2=1$, $D_i=D_i(2)$

Now let us restrict this equation to comparisons between T2 and T1, and T2 and T0:
\begin{align}
\label{PODsplit1}
D_i=D_i(1)+ Z_i^2 \times \big( D_i(2)-D_i(1)\big) \quad \forall i s.t. \bar{Z}_i^0=1\\
\label{PODsplit2}
D_i=D_i(0)+ Z_i^2 \times \big( D_i(2)-D_i(1)-D_i(0)\big) \quad \forall i s.t. \bar{Z}_i^1=1
\end{align}


<!-- \underbrace{\left(1-(Z_i^1+Z_i^2)\right)D_i(0)+Z_i^1D_i(1)}_{=0} -->
Equation (\ref{PODsplit1}) is standard and meaningful. The instrument $Z^2$ reveals the right potential outcomes. However, equation (\ref{PODsplit2}) does not. A clear causal parameter can only be defined over the sample of informed parents if we think that information did not change compliance with our support. Intuitively, we don't know who would have accepted our help in group T1 and T0. The instrumental variable strategy uses the share of compliers in T2 to infer the share of compliers in the comparison group. If information had an effect at least on some families, then T0 is simply not a good comparison group. For instance, some families in $T1$ may have found enough resources in the information to register early and refused our help. But they might have accepted our help had they not receive our information treatment. When we consider T2 and T1, such families are considered *never-takers* in the terminology of @AngristEtAl1996. This is relevant, and offering help likely has no other effect on outcomes but through participation.
But in comparison with T0, such families would be a form of *defiers* and an IV estimators would not recover causal impacts, unless we assume strong additional exclusions restrictions in this first stage: 
$$
D_i(z)=D_i(0) \forall z\in\{0,1\}
$$ 
 and in the second stage. 
<!--  However, under this hypothesis, there are testable implications that may allow to reject this hypothesis\todo{Je suis pas encore complètement au clair sur ça faudrait que je réfléchisse plus et je manque un peu de temps}. -->

Let us make clear how observed outcomes relates to potential outcomes, instruments and compliance.

\paragraph{Potential outcomes with support}

Potential outcomes are defined over the product set of potential participation and instruments and we denote them $Y_i(d,z)$ with $d$ and $z \in \{0,1,2\}$, so there are 9 potential outcomes. However, our design allows to eliminate several :

$$
Y_i(2,0)=Y_i(0,1)=Y_i(2,1)=Y_i(1,0)=\emptyset
$$

The first four cases do not exist because of one-sided non-compliance which eliminates these potential defiers, the fifth case is excluded because all those who were offered assistance had information first and the last case is excluded by our information protocol^[Only those in T1 received information.].

 - $Y_i(2,2)$ is the outcome of compliers when treated
 - $Y_i(1,2)$ is the outcome of never-takers among those who received information.
 - $Y_i(1,1)$ is the outcome of T1 and, by SUTVA: $Y_i(1,1)=Y_i(1)$
 - $Y_i(0,0)$ is the outcome of T0 and, by SUTVA: $Y_i(0,0)=Y_i(0)$

For the two first potential outcomes, we need an additional hypothesis to retrieve $Y_i(2)$:

:::{.hypothesis #exclusion name="Exclusion restrictions"}

Among those who receive the information treatment, offering support has no other effect on outcomes but through the assistance provided.
Formally, 
\begin{equation}
Y_i(d,1)=Y_i(d,2)=Y_i(d)\quad\forall i\in \bar{Z}^0_i=1,\forall d \in \{1,2\}
\end{equation}

:::



With these notations, we can define our target parameters.




\subsubsection{Target parameters}

<!-- Question \ref{} -->





\paragraph{Intention to treat parameters}

A first parameter of interest is the intention to treat effect of offering additional support to those who already received information as:

:::{.definition #ITTS name="Average effects of offering additional support"}

$$
ITT(2)=\esp{Y_i|Z_i^2=1}-\esp{Y_i(1)|Z_i^2=0}\quad \forall i s.t. \bar{Z}^0_i=1
$$
$ITT(2)$ is defined for individuals that are not in the control group T0. Therefore, $Z_i^1=1$ for everyone in this subsample. Note that we can also compare T2 with T0 in intention to treat to capture the effect of the bundled intervention. 

We are also interested in conditional intention to treat effects :
$$
ITT_x(2)=\esp{Y_i|Z_i^2=1,\mathbf{X}=\mathbf{x}}-\esp{Y_i(1)|Z_i^2=0,\mathbf{X}=\mathbf{x}}\quad \forall i s.t. \bar{Z}^0_i=1
$$


:::


Estimating these parameter provide a first answer to question \ref{RQ1} and \ref{RQ1a}. But it does not show the effect on those who receive our support. 

To answer question \ref{RQ2}, we need to compare the effect on T2 vs T1 with T1 vs T0.

We define the average effect of information on any outcome $Y \in \mathbf{Y}$ as: 

:::{.definition #ITTI name="Average effects of information"}

$$
ITT(1)=\esp{Y_i(1)-Y_i(0)}\quad \forall i s.t. \bar{Z}^2_i=1
$$
$ITT(1)$  is defined for individuals that are not in T2.

:::


These two target parameters constitute a family of 2 results for which we want to test $\mathcal{H}^f$:

1) if any of the two is different from 0
2) if T2 is different from T1.

We formally test these hypothesis accounting for the FWER using generalized linear hypothesis testing following @HothornEtAl2008. We also compute confidence interval of the difference and interpret the set of plausible values.






<!-- Similarly, we define  -->
<!-- Note that contrary to definition \ref{def:ITTI}, only one potential outcome is revealed. The left conditional expectation is indeed the average of compliers and never-takers. -->

<!-- Furthermore, we are interested in the overall intention to treat effect of any treatment: -->

<!-- :::{.definition #ITT name="Average effects of proposing any intervention"} -->

<!-- $$ -->
<!-- ITT=\esp{Y_i|Z_i^1=1}-\esp{Y_i(0)|Z_i^1=0} -->
<!-- $$ -->
<!-- Note that $Z_i^1=1$ include T1 and T2 and the "active" group is twice as large as the comparison group.  -->
<!-- ::: -->
Note that contrary to definition \ref{def:ITTI}, only one potential outcome is revealed in definition \ref{def:ITTS}. The left conditional expectation is indeed the average for compliers and never-takers.


We are interested in the average direct effect of the support offered to parents on those who accepted it. It requires the estimation of the first stage which we define now.

\paragraph{First stage: The demand for help and decision making}

:::{.definition #FirstStage name="First stage"}

\begin{itemize}
\item {\bf Average demand}: Let $\pi_i=D_{i}(2)-D_i(1)$ and let  $$\pi \equiv \esp{\pi_i} =\esp{D_{i}(2)-D_i(1)}$$ be the average effect of proposing help on receiving help.
\item {\bf Block-specific demand}: let $\pi_b=\esp{D_{i}(2)-D_i(1)|B_i=b}$ be the average effect of proposing help on receiving help within block $b$.
\end{itemize}

$$
\pi=\sum_b pr(B_i=b)\esp{D_{i}(2)-D_i(1)|B_i=b}
$$
The average effect is the weighted average of the within-block effect with proportion of observations in each block as weights.

:::

The first stage effect captures the demand for help in choosing and applying for formal childcare solutions. The population who accept our help are called *compliers*. 
<!-- Indeed, they comply with our treatment but also decide that they want to apply to formal childcare for sure. Importantly, we do not restrict heterogeneity in compliance.  -->

\subparagraph*{Remarks}

The first stage effect could be more formally analyzed if we think of it as a threshold choice function in a generalized Roy Model [@HeckmanVytlacil2005]. In the basic framework, the agent selects into treatment if the net utility from doing so is positive. This choice depends on the information set, subjective expected costs, benefits and so on. Importantly, such formalization is actually numerically equivalent  to the LATE framework of @AngristEtAl1996  [See @MogstadEtAl2018;@KlineWalters2019]. However, generalized Roy models can recover more general causal parameters under additional hypotheses. In our framework, participation decision reflects subjective cost-benefit evaluations and the joint decision of accepting help and choosing childcare arrangements. Therefore,  modelling the *conditional average encouragement effect function* $\pi(\mathbf{x})=\esp{D_{i}(2)-D_i(1)|\mathbf{X}=\mathbf{x}}$ with a set of covariates that capture information set, perceived benefits, costs or views on formal childcare, in a more structured model can be very informative. Second,  Generalized Roy models allow to estimate marginal treatment effects and treatment effect heterogeneity over the distribution of the propensity to accept help.
 
This formalisation is left for futur work and we focus on the identification of the LATE parameters.
 

<!-- \todo[inline]{Coralie, Carlo, Laudine, tout ça me donne une idée... -->
<!-- Je crois qu'il faut comparer compliance with treatment in T2 with application to any childcare in T1 ; en disant que compliance pousse la décision en baissant le coût ; dire que on observe $\tilde{D}$ une mesure des candidatures à formal childcare. Le but c'est de faire un modèle de Roy sur $\tilde{D}$ dans lequel on mesure l'effet du traitement T2 et de variables behavioral {\bf guidée par la théorie}. Donc un choix de covariates. Il y a déjà les blocks dans l'équation ;  donc les scores de costs, knowledge etc. budget constraint,...  ça nous permet d'avoir la discussion sur effet substitution ou complémentarité ET faire un modèle behavioral de choix qui en plus derrière nous permet d'identifier des treatments effects qui ont du sens. -->

<!-- On a e, tête un gene roy model qui teste ce qui est un paramètre intéressant qu'on formalisera qu'on formalisera par une description de ce modèle dans le papeir}  -->












\paragraph{Effects of support on those who accepted it}


:::{.definition #LATE name="Average treatment effect on assistance compliers"}

\begin{equation}
\label{eq:ATT}
ATT(1)=\esp{Y_i(2)-Y_i(1)|D_i(2)>D_i(1)}
\end{equation}

$ATT(1)$ is the average treatment effect on those who accepted support and information but who would otherwise receive information: the low-cost intervention.

:::

This target parameter allows to answer our main research questions and document mechanisms when estimated over intermediary outcomes. 





We also use the results proved by @Abadie2003 and recently revisited by @SloczynskiEtAl2022a and @SloczynskiEtAl2022c.

Under hypotheses \ref{hyp:indep} and \ref{hyp:exclusion}, we recall the following lemma holds:

:::{.lemma #Abadie name="Abadie 2003, pp. 236-237"}

Let $g(\cdot)$ be any measurable real function of $(Y, D, X)$ such that $\mathrm{E}|g(Y, D, X)|<\infty$. Define
$$
\begin{aligned}
\kappa_0 & =(1-D) \frac{(1-Z)-(1-p(X))}{p(X)(1-p(X))}, \\
\kappa_1 & =D \frac{Z-p(X)}{p(X)(1-p(X))} \\
\kappa=\kappa_0(1-p(X))+\kappa_1 p(X) & =1-\frac{D(1-Z)}{1-p(X)}-\frac{(1-D) Z}{p(X)} .
\end{aligned}
$$
Under Assumptions \ref{hyp:indep} and \ref{hyp:exclusion},
\begin{enumerate}
\item $\mathrm{E}\left[g(Y, D, X) \mid D_1>D_0\right]=\frac{1}{\mathrm{P}\left(D_1>D_0\right)} \mathrm{E}[\kappa g(Y, D, X)]$. Also,
\item  $\mathrm{E}\left[g\left(Y_0, X\right) \mid D_1>D_0\right]=\frac{1}{\mathrm{P}\left(D_1>D_0\right)} \mathrm{E}\left[\kappa_0 g(Y, X)\right]$, and
\item $\mathrm{E}\left[g\left(Y_1, X\right) \mid D_1>D_0\right]=\frac{1}{\mathrm{P}\left(D_1>D_0\right)} \mathrm{E}\left[\kappa_1 g(Y, X)\right]$.
\item Moreover, $(\mathrm{a}-\mathrm{c})$ also hold conditional on $\mathrm{X}$.
\end{enumerate}


:::

This Lemma is very powerful, and has many useful applications to recover interesting parameters. For instance, by setting $g\left(X_i, Y_i(d)\right)=X_i$, an IV procedure yields the average of any predetermined covariate $X_{i}$ for compliers. Therefore, we can characterize the complier population and see if they differ from other comparison groups. Similarly, we can estimate the mean for never-takers by regressing $X_{i}(1 − D_{i})Z_{i}$ on $(1 − D_{i})Z_{i}$. 

More importantly, we can estimate the distribution of the missing potential outcomes for compliers. When $Y$ is a continuous variable such as information scores and so on, by setting $g\left(X_i, Y_i(d)\right) = \one{Y_i \leq y}$ for a constant $y$ and each value of $d$, we obtain the complier cumulative distribution functions of $Y_i(2)$ and $Y_i(1)$ evaluated at $y$. 


<!-- \paragraph{Policy relevant causal effects of interest} -->

<!--  We simplify the problem and only consider 3 childcare arrangements : parental care,  childminders and daycares. Say we estimate the effect on access to daycare. -->

<!-- Following our roadmap, we define our outcome first: -->

<!-- Let $Y=\one{ECS}$ be the dependent variable that equals one when the family has access to formal childcare and 0 otherwise. -->

<!-- Then, under hypotheses \ref{hyp:indep} and \ref{hyp:exclusion}, we can estimate the average treatment effect on participants by 2SLS of equations (\ref{eq:2SLS}) which estimate the parameters of defintion \ref{eq:ATT}: $ATT(1)$. For the sake of the argument, let us assume that our administrative support is very effective and increases access to formal childcare, and to daycares in particular. -->

<!-- With regard to our main research questions, this result would be interpreted as a success of the program. -->
<!-- This positive effect would mean that we changed the demand size, structure and successfully increased access to those we helped. -->
<!-- Because we have no effect on supply, that would also imply that other parents were crowd-out or used other childcare arrangement. -->
<!-- In any case, it would mean that the new equilibrium on the childcare market is different, and matched different families to different childcare arrangement. However, it is not the same policy implication if our treatment switches childcare arrangement from childminders to daycare or from parental care. -->

<!-- In the literature, this problem is often referred to as *substitution bias* [see e.g. @HeckmanEtAl1999]. For instance, @KlineWalters2016 show that the disappointing evaluations of Early Head Start\footnote{Head Start is a program of the United States Department of Health and Human Services that provides comprehensive early childhood education, health, nutrition, and parent involvement services to low-income children and families} (EHS) in the US on children achievement was actually hiding heterogeneous treatment effect among latent complier types with different counterfactual alternatives. In the absence of EHS, some children would have been cared for by their parents while others would have been cared for in other childcare arrangement that are close substitute to head start.  @BerkesBouguen2019 find a similar situation while estimating the impact of building preschools in Cambodia where there also exist informal substitutes. -->

<!-- The problem is not about identification for the complier group but about interpretation when treatment effect is heterogeneous. -->
<!-- To be precise, the average treatment effect for participants (LATE) on access to daycare can be decomposed into two weighted sub-LATEs for two sub-groups of compliers : -->

<!-- - **C switcher** those moving from childminder to daycare, -->
<!-- - **P switcher** those moving from parental care to daycare -->

<!-- Let us change the outcome to divide the alternative to daycare: -->
<!-- $$ -->
<!-- \tilde{Y}=\left\{\begin{matrix} -->
<!-- C:=&\text{Childminder}\\ -->
<!-- D:=&\text{Daycare}\\ -->
<!-- P:=&\text{Parent}\end{matrix} -->
<!-- \right. -->
<!-- $$ -->
<!-- Consistent with our previous notations those in daycares have $\tilde{Y}_i(2)=D$. For them, unobservable individual treatment effects are $\tilde{Y}_{2i}(2)-\tilde{Y}_{2i}(0)$ and the question is: Is $\tilde{Y}_i(0)=C$ or $\tilde{Y}_i(0)=P$ ? -->


<!-- Figure \ref{fig:compliers} illustrate this example to build intuition. -->
<!-- On the left, we represent a partition^[In proportion] of childcare arrangements in the information group. In this situation, we imagine that a large share of families uses parental care as their main childcare arrangement and another large share uses childminders. In between, a fair share gets to use daycare. Now, if these same families were supported in their application process, we might get something like the right column. -->

<!-- In this illustration, administrative support increases access to formal childcare but through a redistribution between childminders and daycare centers. Compliers who access formal childcare come from the two sub-populations of P and C-switchers. -->

<!-- It is easy to show as in @KlineWalters2016^[This result actually comes from the original paper by @ImbensAngrist1994 where they discuss multi-valued treatment.] that equation (\ref{eq:ATT}) can be decomposed as a weighted average of two sub-LATEs: -->


<!-- \begin{align}\label{sublate} -->
<!-- LATE_\delta= S_0 Late_{\delta_2} + (1-S_0)Late_{\Delta} -->
<!-- \end{align} -->

<!-- Where $Late_{\delta_2}=\esp{Y_i(2)-Y_{i}(1)|Y_i(2)=D,Y_i(1)=P}$ and $Late_{\Delta}=\esp{Y_i(2)-Y_{i}(1)|Y_i(2)=D,Y_i(1)=C}$ are the local average treatment effect on compliers with different next best alternative and: -->
<!-- \[ -->
<!-- S_0=\frac{Pr\big(Y_i(2)=D,Y_i(1)=P\big)}{Pr\big(Y_i(2)=D,Y_i(1) \in \{D\cup C\} \big)} -->
<!-- \] -->
<!-- is the fraction of compliers who would have chosen parental care. -->

<!-- With only one instrument, the sub-LATE are not identified but through additional hypotheses. We need to use extra information on next best alternative [@KirkeboenEtAl2016] or modified monotonicity assumptions [@BehaghelEtAl2013;@HeckmanPinto2018]. Our paper will formally define this model but we essentially control for baseline intention to use for specific childcare solutions. -->


<!-- \subparagraph{Irrelevance and next-best alternative}: -->

<!-- Following @KirkeboenEtAl2016, we can identify the sub-lates if we use information about individuals next best alternatives with weak assumptions about individuals preferences. -->
<!-- First we make an assumption about irrelevance: the idea is that if switching $z_1$ (resp. $z_2$)  from 0 to 1 does not make the family get childminder C (resp. D), then it does not make her choose daycare D (resp. C) either\footnote{This is again a way to say there are no switchers.}. Formally, if $d_1(z_1=1)= d_1(z_1=0)=0 \Rightarrow d_2(z_1=1)=d_2(z_1=0)$ ; $d_2(z_2=1)=d_2(z_2=0)=0 \Rightarrow d_1(z_2=1)=d_1(z_2=0)$. -->
<!-- On its own, this assumption does not solve the issue but together with information on the next best alternative it does. The intuition is straightforward: by conditioning on the next-best alternative, individuals who are induced to choose one childcare arrangement because of a change in the instrument come from a particular alternative arrangement. Conditioning on the next best intervention and assuming irrelevance we get: -->

<!-- \begin{equation} -->
<!-- \begin{array}{ll} -->
<!-- \beta_1=&\esp{\delta_1|d_1(z_1=1)-d_1(z_1=0)=1,d_2(z_2=0)=0}\\ -->
<!-- \beta_2=&\esp{\delta_2|d_2(z_2=1)-d_2(z_2=0)=1,d_1(z_1=0)=0}\\ -->
<!-- \end{array} -->
<!-- \end{equation} -->



<!-- We think that these composition effects are important to document, but we need to formally define what they are. -->


<!-- ```{=latex} -->
<!-- \begin{figure}[h!] -->
<!-- \caption{The impact of instrument $Z^2$ on compliance and outcomes of different sub-groups.}\label{fig:compliers} -->
<!-- \begin{center} -->
<!-- \begin{tikzpicture} -->

<!--         %Left block -->
<!--     \fill[fill=blue!20] (0,0) rectangle (2,1); -->
<!--     \fill[fill=blue!40] (0,1) rectangle (2,2.5); -->

<!--     \fill[fill=orange!30] (0,2.5) rectangle (2,4); -->
<!--     \fill[fill=teal!40] (0,4) rectangle (2,6); -->
<!--     \fill[fill=teal!20] (0,6) rectangle (2,9); -->


<!--         % right block -->
<!--     \fill[fill=blue!20] (4,0) rectangle (6,1); -->
<!--     \fill[fill=orange!50] (4,1) rectangle (6,2.5); -->
<!--     \fill[fill=orange!30] (4,2.5) rectangle (6,4); -->
<!--     \fill[fill=orange!50] (4,4) rectangle (6,6); -->
<!--     \fill[fill=teal!20] (4,6) rectangle (6,9); -->

<!--         % Left labels -->
<!--     \draw (1,.5) [black,midway] node{\footnotesize Childminder}; -->
<!--     \draw (1,1.75) [black,midway] node{\footnotesize Childminder}; -->
<!--     \draw (1,3) [black,midway] node{\footnotesize Daycare}; -->
<!--     \draw (1,5) [black,midway] node{\footnotesize Parents}; -->
<!--     \draw (1,7) [black,midway] node{\footnotesize Parents}; -->

<!--         % Right labels -->
<!--     \draw (5,.5) [black,midway] node{\footnotesize Childminder}; -->
<!--     \draw (5,1.75) [black,midway] node{\footnotesize Daycare}; -->
<!--     \draw (5,3) [black,midway] node{\footnotesize Daycare}; -->
<!--     \draw (5,5) [black,midway] node{\footnotesize Daycare}; -->
<!--     \draw (5,7) [black,midway] node{\footnotesize Parents}; -->

<!--         % Dashed lined -->
<!--     \draw [dashed,black](0,1) - - (8.5,1) ; -->
<!--     \draw [dashed,black](0,6) - - (8.5,6) ; -->
<!--     \draw [dashed,black](0,2.5) - - (8.5,2.5) ; -->
<!--     \draw [dashed,black](0,4) - - (8.5,4) ; -->

<!--         % Box above with instruments value -->
<!--     \node[draw] at (1,9.5) {{\footnotesize $Z^{2}_i=0$}}; -->
<!--     \node[draw] at (5,9.5) {{\footnotesize $Z^2_{i}=1$}}; -->

<!--             %Types -->
<!--         \draw (7.5,.5) [black,midway] node{\footnotesize C always-takers}; -->
<!--         \draw (7.5,1.5) [black,midway] node{\footnotesize C compliers}; -->
<!--         \draw (7.5,3) [black,midway] node{\footnotesize D always-takers}; -->
<!--         \draw (7.5,5) [black,midway] node{\footnotesize P compliers}; -->
<!--         \draw (7.5,7) [black,midway] node{\footnotesize P always-takers}; -->

<!--             % -->
<!--        \draw [decorate,decoration={brace,amplitude=10pt,mirror,raise=4pt},yshift=0pt] -->
<!--  (8.5,4) -- (8.5,6) node [black,midway,text width=1.5cm,xshift=1.5cm] {\footnotesize -->
<!--  {$S_0$ $~~(LATE_{P})$}}; -->
<!--         \draw [decorate,decoration={brace,amplitude=10pt,mirror,raise=4pt},yshift=0pt] -->
<!--  (8.5,1) -- (8.5,2.5) node [black,midway,text width=1.5cm,xshift=1.5cm] {\footnotesize -->
<!--  {$1-S_0$ $~(LATE_{C})$}}; -->

<!--   \draw [decorate,decoration={brace,amplitude=10pt,mirror,raise=4pt},yshift=0pt] -->
<!--  (10.5,2) -- (10.5,5) node [black,midway,xshift=3.5cm] {\footnotesize -->
<!--  {$ATT(1)=S_0LATE_{P}+(1-S_0)LATE_{C}$}}; -->

<!-- \end{tikzpicture} -->
<!-- \end{center} -->
<!-- \end{figure} -->



<!-- ``` -->







\paragraph{Selection bias}



We simply estimate average (conditional) differences between families in T2 by treatment status *i.e.* \underline{as-treated analysis} to gauge selection bias [@HeckmanEtAl1998]. We also compare compliers and never takers characteristics estimated with the previous method.






We now move to our estimation strategy for these parameters.



## Estimation strategy

We need to define our empirical strategy to estimate:

1) intention to treat parameters
2) treatment effects on compliers
3) heterogeneous treatment effects

And inference for hypothesis testing. We explain our general method to deal with non-response in the baseline. Our sample may suffer from attrition between baseline, endline and follow-up. We define our strategy to test and correct for differential attrition.




\subsubsection{Roadmap}

A lot of our target parameters are identified and can be estimated by simple comparisons of weighted averages between treatment arms across  across blocks. Regressions allow to estimate such weighted average,  compute appropriate standard errors and add additional control variables. 

For that, we define a simple roadmap that we can use with each family of outcomes:

\begin{enumerate}
\item \label{problem} We define the main measurement and alternative definitions and which comparison groups should be retained.
\item \label{baseline} We run a baseline estimation with treatment and only block fixed effect.
\item \label{robustness} We run additional estimations with control variables to improve precision.
\item \label{Heterogeneity} We run separate estimations on predefine subgroups.
\end{enumerate}

With this roadmap and the numerous research questions to test, we also need to control for familywise error rates associated with our statistical tests. 

\subsubsection{Inference}

Although individual observations are likely correlated within clusters such as maternity wards, our decision regarding inference depends primarily on our design [@AbadieEtAl2020;@AbadieEtAl2022]. We expect heterogeneous treatment effect within blocks and therefore, follow @deChaisemartinRamirez-Cuellar2020a and use cluster-robust standard errors adjusted at the block level.
Within each family of outcomes the chances of type-II error increase and the test statistics based on point-estimate standard error will over-reject the null hypothesis of no treatment effect. 
Instead, we consider testing the $K$ null hypotheses. $H_0^{1}, \ldots, H_0^K$ individually and require that the familywise error rate, i.e., the probability of falsely rejecting at least one true null hypothesis, is bounded by the nominal significance level $\alpha=.05$. We use adjusted $p$-values to describe the decision rules. Adjusted $p$-values are defined as the smallest significance level for which one still rejects an individual hypothesis $H_0^j$, given a particular multiple test procedure [@HothornEtAl2008]. By construction, we can reject an individual null hypothesis $H_0^k, k=1, \ldots, K$, whenever the associated adjusted $p$-value is less than or equal to the pre-specified significance level $\alpha$, i.e., $p_k \leq \alpha$. The adjusted $p$-values. 

Consistent with our pre-registration and power calculations,
we use $\alpha=.05$.




\subsubsection{Baseline data and non-response}

Our baseline database includes 1849 mothers assigned in each treatment arms. All important question for the design were mandatory. For the other variables, parents were usually given the opportunity to not answer or say they don't know. When we use these variables in the analysis, we include dummies for such cases.
When variables are quantitative but values are missing, we include a dummy for missing and impute the mean value within block.

Importantly, all continuous variables used as a regressors are demeaned although we avoid using continuous regressors and we generally use dummified variables (through quantiles for instance).

\subsubsection{Attrition}
\label{sec:attrition}
Outcomes are measured in the second survey (called endline survey) between mid-October and late December through CATI.
The research team will exert different efforts to maximize the response rate and reach the highest response rate. For instance, respondents to the endline survey are offered a voucher of 10€ to compensate for their time loss. In our pre-registration, we anticipated an average answer rate of 75 %. We follow standard practices to correct for imbalance [see for instance @Doyle2020a].

Let $R_i=\one{Answer}$ denote the individual survey response status.

1) We first run a sanity check and estimate the following equation with OLS:
$$
R_i=\sum_b \gamma_b B_{i} +\delta_1 Z^1 +\delta_2 Z^2+\varepsilon_i
$$

2) We jointly test $\hat{\delta_1}=\hat{\delta_2}=0$
3) We run a fully saturated version of the previous regression and
4) We predict response status to construct corrective weights using standard functions of the inverse predicted probability and treatment arms.
5) We select baseline attributes that predict response using double lasso 
6) We generate an alternative set of weights from the model with covariates selected using double lasso and more individual characteristics as a robustness check.

We present unweighted results and estimations with both sets of weights.

We also collect informations on how many calls we make to before reaching a household etc. This might be used to correct for endogenous non-response following @BehaghelEtAl2015. 

\subsubsection{Models for intention to treat parameters}


\paragraph{Baseline models}




$ITT$ parameter can be simply estimated by OLS with block fixed effects :

\begin{equation}
Y_{i}=\sum_{b}\alpha_{b}B_{i}+\beta Z_{i}+\varepsilon_{i},\quad i  \in \bar{Z}
(\#eq:ITTCross)
\end{equation}


Where $\alpha_{b}$ estimates average difference in outcome across blocks and $\beta$ estimates a treatment-variance weighted average of block average intention to treat. We restrict over the relevant comparison groups $\bar{Z}$ corresponding to the ITT we define.

In most settings, the treatment-variance weighting of OLS is no issue since we compare to groups with the same treatment probability. However, some blocks may be small and slightly imbalanced. 
We therefore adopt a doubly-robust approach where :

1) We first regress $Z^1_i$ on block fixed effects 
2) predict assignment probabilities for each block from the previous model
3) construct inverse probability weights for individuals of T2 and T1
4) run a weigthed version of the previous equation.



\paragraph{Robustness}

The main motivation for adjusting for covariates in RCTs is that the precision of the estimated average treatment effect can be improved if the covariates are sufficiently predictive of the outcome [@Lin2013]. 
Randomisation ensures there are no correlation in the population between $Z_{i}$ and the covariates $\mathbf{X}_{i}$, which is sufficient for the lack of bias from including or excluding the covariates [@AtheyImbens2017a]. We follow @NegiWooldridge2021 recommendation and use pooled regression. In particular, including baseline outcomes (centred or in dummies) may increase precision while leaving the p-limit of the ITT coefficients unchanged.
We then estimate the following equation using OLS:

\begin{equation}
(\#eq:ITTStacked)
Y_{i}=\mathbf{B}\prime\alpha +\beta Z_{i}+ \mathbf{X}\prime \rho+\varepsilon_{i}
\end{equation}

We use double lasso to select variables.


\paragraph{Heterogeneity}

To assess heterogeneity, we simply run separate regression over subgroups of interest. To account for simultaneous inference and test equalities of treatment across groups, we *stack* the separate models and run a single estimation. We  use the method described by @HothornEtAl2008 which assume joint normality of the treatment effect and use the variance covariance estimated from the stacked equation to correct for simultaneous inference. 



\subsubsection{Models for T2 against T1}


\paragraph{First stage effects}


The average effect of offering support on take-up can be obtained estimating the following equation using OLS:

\begin{equation}
\label{eq:FSmean}
D_{i}=\sum_b\alpha_{b}B_{i}+\pi Z^2_{i}+\varepsilon_{i}, \quad i s.t.  \bar{Z}_i^0=1
\end{equation}
Where $\pi$ is the average demand for assistance among those who received information  $i.e$ $\pi=E_b\Big(E\left(D_{i}(2)|B_i=b\right)\Big)$.
It estimates the average effect of encouragement on participation as a weighted average of the within-block average effects, with weights proportional to the product of the fraction of observations in the block and the probabilities of receiving and not receiving the treatment.

The following equation can also be estimated using OLS: 
\begin{equation}
\label{eq:SaturatedFs}
D_{i}=\sum_bZ^2_{i}B_{i}\pi_{b}+\varepsilon_{i},\quad i s.t. \bar{Z}_i^0=1
\end{equation}

The recent work of @BlandholEtAl2022, @SloczynskiEtAl2022a and @SloczynskiEtAl2022c revisit the use of 2SLS to estimate the LATE and show that the only specifications that have a LATE interpretation are “saturated” specifications that control for covariates non-parametrically or with restrictive parametric assumption.

Equation (\ref{eq:SaturatedFs}) is fully saturated^[This first stage is saturated because it includes a parameter for each value of $\esp{D_{i} | Z_{i}, b_{w}}$.] and estimate one effect of Z by block such that $E(\pi_{b})=E(D_{i}(2)|B_i=b)$. The OLS estimation is equivalent to a non parametric estimation of the first stage.

\paragraph{Average effects on compliers}

With independence, a first stage effect with one sided non-compliance and exclusion, 
the  average treatment effects on compliers  are identified as the ratio of the expected  difference in outcome by treatment arms over the expected first stage effect [@AngristEtAl1996]:

\begin{equation}
(\#eq:LATEm)
\begin{array}{lll}
LATE(Y)&=&\frac{
\left(E_b\left(
      Y_{i}|Z^2_{i}=1,B_i=b\right)
      -E_b\left(
      Y_{i}|Z^2_{i}=0,B_i=b\right)
      \right)}
      {\left(
      E_b\left(
      D_{i}|Z^2_{i}=1,B_i=b\right)
      \right)
      -\underbrace{
      \left(
      E_b\left(
      D_{i}|Z^2_{ijc}=0,B_i=b\right)
      \right)
      }_{=0~\text{one sided non-compliance}}}\\
&=&\frac{\left(ITT(2)\right)}{E_b\left(\pi_{b}|B_i=b\right)}
\end{array}
\end{equation}

Because of one-sided non compliance, these parameters correspond to the average treatment effect on the treated [@FrolichMelly2013a].
These parameters can be estimated via the following 2SLS system of equation:

\begin{equation}
(\#eq:2SLS)
2SLS~\left\{ \begin{array}{cc}
Y_{i}=&\sum_b \alpha_{b}B_{i}+\delta D_{i}+\mu_{i}\\
D_{i}=& \sum_b \gamma_{b}B_i+\sum_b B'_{b}Z^2_{i}\pi_{b}+\epsilon_{i}\\
\end{array} \right. 
\end{equation}
adjusting standard errors for clustering at the block level.


<!-- \subsubsection{Additional analysis} -->


\paragraph{Compliers characteristics and distribution of potential outcomes}
@AngristEtAl2023 conveniently summarize the use of instrumental variable in economics of education and recall many important results.
In our setting comparing T2 and T1, the population contributing to the instrumental variable analysis contains only never-takers and compliers in this setting. The population with $D_i = 0$ and $Z^2_i = 1$ are never-takers, $D_i = Z^2_i = 1$ are compliers, while the group with $D_i = Z^2_i = 0$ is a mixture of never-takers and compliers. However, their relative sizes are identified as the complier share equals the size of the first stage.

Under assumptions \ref{hyp:indep} and \ref{hyp:exclusion},  @Abadie2003 propose a simple 2SLS procedure for characterizing compliers, described by:

\begin{subequations}
\begin{align}
 \label{eq:abadie2}
g\left(X_{i}, Y_{i}\right) \times \one{D_{i}=d} & =& \sum_b \alpha_{b}B_{i}+\gamma_d \one{D_{i}=d}+\mu_{i}\quad d \in\{0,1\} &   \\
\label{eq:abadie1} \one{D_{i}=d}&=& \sum_b \eta_{b}B_{i}+\sum_b Z^2_{i}\times B_{i}\pi_{b}+\epsilon_{i}&
\end{align}
\end{subequations}
where $g\left(X_{i}, Y_{i}\right)$ is any function of family baseline characteristics $X_{i}$ and outcomes $Y_{i}$.
Note that the first stage is fully saturated and $\pi_{w}$ recover the block-specific first stage effects so that the projection of the first stage estimate correspond to the conditional expectation function and the TSLS estimate correspond to a LATE-like parameter (see Theorem 3 in @AngristImbens1995).
Setting $d = 1$ in (\ref{eq:abadie1}) and (\ref{eq:abadie2}) means using $Z^2_{i}$ as an instrument for $D_i$ in an IV procedure with $g\left(X_{i}, Y_{i}\right)$ multiplied by $D_{i}$ as the outcome. Setting $d = 0$ means we use $Z_{i}$ to instrument $(1 − D_{i})$ in an equation with $g\left(X_{i}, Y_{i}\right)(1 − D_{i})$ as the outcome
which recover characteristics of treated and untreated compliers:
\begin{equation}
\gamma_d=E\left[g\left(X_{i}, Y_{i}(d)\right) \mid D_{i}(2)>D_{i}(1)\right], \quad d \in\{0,1\}
\end{equation}

By setting $g\left(X_i, Y_i(d)\right)=X_i$, the IV procedure produces the average of any predetermined covariate $X_{i}$ for compliers within a block, and I estimate never-taker means by regressing $X_{i}(1 − D_{i})Z_{i}$ on $(1 − D_{i})Z_{i}$ with block fixed effect.

With this transformation, I can also estimate the distribution of the missing potential outcomes for compliers. By setting $g\left(X_i, Y_i(d)\right) = \one{Y_i \leq y}$ for a constant $y$ and each value of $d$, I obtain the complier cumulative distribution functions of $Y_i(1)$ and $Y_i(0)$ evaluated at $y$. 

More specifically,  @AbdulkadirogluEtAl2018 propose to use a symmetric kernel function $g\left(X_i, Y_i(d)\right) = \frac{1}{h} K(\frac{Y_i−y}{h})$ in equation (\ref{eq:abadie2}) to estimate the density of the potential outcomes for compliers at $Y=y$. $K(\cdot)$ is a symmetric kernel function maximized at zero and h is a bandwidth that shrinks to zero asymptotically. We follow @AbdulkadirogluEtAl2018 and evaluates complier densities at a grid of 100 points with kernel bandwidth defined as $h = 1.06 \times N^{\frac{−1}{5}}\sigma_d$, where $N$ is the sample size and $\sigma_d$ is the standard deviation of the potential outcome. 


<!-- \paragraph{Data driven exploratory analyses} -->


\section{Analysis and hypothesis testing}
\label{sec:stat}

Now that our empirical strategy is well defined and all causal parameters introduced, we can explain how we can answer our main research questions.

Question \ref{RQ1} translates in an analysis of the average effect of our treatments on a measure of demand for and access to ECS. Question \ref{RQ1a} assesses overall treatment effect heterogeneity by socio-economic background. It can be estimated by comparing pooled treatment effects between blocks of low and high SES. 

Question \ref{RQ2} relates to the treatment effect heterogeneity between treatment arms. Question \ref{RQ2a} assesses the differential impact of T2 compared to T1 by socioeconomic background.



<!-- Questions \label{RQ1} and \label{RQ1a} are answered when we estimate the effects of our interventions on the family of proximate outcomes : application behaviour.
Questions \label{RQ2} and \label{RQ2a} are answered when we estimate the effects of our interventions on the family of final outcomes : access to formal childcare.
Furthermore, our logic models motivates additional estimations of the effect of our interventions on the family of intermediary outcomes.

Together, these results help understand mechanisms that may hinder or foster access to formal childcare. We also define hypotheses on treatment effect heterogeneity.
We start by stating our hypotheses on the set of proximate outcomes, then on the set of intermediary outcomes. We discuss the link between these two sets of results. Finally, we introduce our hypotheses on final outcomes and extensively discuss policy implications. Ultimately, this discussion calls for additional modelling assumptions to answer the policy relevant parameters. -->

\subsection{Proximate outcomes: application behaviors}

\subsubsection{Definition of outcomes and set of covariates}

We expect our intervention to change to components of application behaviors previously noted \(\mathbf{\tilde{D}}\) :

\begin{itemize}
\tightlist
\item
  the decision to use ECS (and which ones)
\item
  the number of applications.
\end{itemize}

For this set of outcomes, we use a double-LASSO to choose vectors in $\mathbf{X}_{i}$ among baseline control variables at the parent level (mother and father level of education, employment status, country of birth, baseline level of information, household composition, intention to use ECS, past ECS use, fluency in french, number of children, coverage rate, adherence with traditional norms, amount of family and friends using ECS, access to a computer, age of the mother, whether ECS opening hours fit with parents' working hours, beliefs in ECS returns, gender of the child, level of trust in daycare centers, perceived costs, perceived opportunity costs and costs on well-being and on the career).


\subsubsection{Treatment effects on Parents' likelihood to apply}

Following our analysis roadmap, we first define measurement for our main outcome which is simply a dummy if parent is registered to any formal childcare.

We use the combination of answers to the endline survey and known applications for those who received administrative support to define a binary variable that equals one when a household applied to any ECS and 0 otherwise. We will assess the veracity of parents' answers before running these analyses.

Because dates of birth are heterogeneous in our sample, some parents may not have registered yet but intend to. Therefore, we will also use an alternative measurement that takes value 1 if parents intent to apply to ECS or have already applied, and 0 otherwise as a robustness check. 


<!-- \paragraph{First elements to answer our first research question} -->

<!-- Question \ref{RQ1} tests the joint intention to treat effect of information + administrative support and we make the following hypothesis: -->
\paragraph{Intention to treat estimates}



-\textbf{Hypothesis 1} (subset \(\bar{Z}^2\)): We hypothesize that the information treatment increases the likelihood that parents apply to at least one ECS.

\begin{itemize}
\tightlist
\item
  We test the null \(\mathcal{H}_1: \hat{\beta_1}=0\) with a one sided test of positive treatment effect.
\end{itemize}



-\textbf{Hypothesis 2}(subset \(\bar{Z}^2\): We hypothesize that offering information and administrative support increases the likelihood that parents applied to at least one ECS.



\begin{itemize}
\tightlist
\item We test the null \(\mathcal{H}_2: \hat{\beta}_{0}=0\) with a one sided test of positive treatment effect of the OLS regression of equation (\ref{eq:ITTCross}).
\end{itemize}

This effect is estimated in intention to treat and simply measures the average differences between T2 and T0. We then estimate this model with covariates.

<!-- Question \ref{RQ2} tests the heterogeneity between T2 and T1. -->
<!-- Our baseline strategy consists in estimating equation (\ref{eq:ITTCross}) with OLS over \(\bar{Z}^2\) and \(\bar{Z}^0\) i.e.~comparing T1 and T0 and T2 and T1 to retrieve the intention to treat parameters. We index the estimations of the ITT parameters \(\beta_g\) with \(g \in \{1,2\}\), the corresponding treatment arms. Note that \(\beta_2\) is computed against parents who also received the information treatment. -->

-\textbf{Hypothesis 3} (subset \(\bar{Z}^0\)): We hypothesize that offering administrative support increase ECS applications compared to information only.

\begin{itemize}
\tightlist
\item
  We test the null \(\mathcal{H}_3: \hat{\beta_2}=0\) with a one sided test of positive treatment effect.
\end{itemize}

We follow the road map and estimate these models with covariates and adjust p-value for the FWER over each pair of test (with or without covariates).

If we reject \(\mathcal{H}_1\), we conclude that the our information  treatment is effective in increasing the likelihood of applying to any ECS.
For this set of outcomes and all the other below, we do not expect sizeable effects of information only because the informational intervention boils down to a few simple messages. This especially if behavioral and administrative barriers are involved. However, given the very low cost of the information-only treatment, even a small positive effect is interesting to detect.

If we reject \(\mathcal{H}_2\), we conclude that the offering information  and administrative support increases the likelihood that
parents applied to at least one ECS.

If we reject \(\mathcal{H}_3\), we conclude that offering administrative support further increases this probability compared to information only.


Importantly, this effect is largely driven by the compliance rate. Indeed, almost all those who accepted the administrative support registered to at least one ECS. It also depends on compliers' behaviour in the absence of treatment. 

\paragraph{Average treatment effect on compliers}

To estimate the effect on compliers, we use random assignment as an instrument for participation.
We estimate equation \ref{eq:2SLS} by 2SLS to retrieve the average treatment effect on compliers. This model also answers hypothesis 3 but retrieve the average effect on those who accepted administrative support. We also test the null \(\mathcal{H}_\delta: \delta=0\) with a one sided test.

Finally, we apply the same strategy in exploratory analysis over types of childcare they registered to and see if treatments fosters registrations in specific ECS types.


\subsubsection{Number of applications}

We want to see if our treatment affected the total number of applications sent per households. We define the total number of applications sent per households as sum of applications sent across type of applications. For instance, if parents applied to municipal daycare and 5 associative daycares, the total number of applications sent will be 6).
<!-- There are two questions that this part of the analysis tries to uncover. -->

<!-- 1) Did administrative support increased the total number of applications across types -->
<!-- 2) Did participants increased/decreased their own efforts to register. -->

<!-- Both questions relate to the underlying mechanisms that could foster access to formal childcare or not. On the one hand, we hypothesize that information and administrative support increased the choice set and facilitated applications. On the other hand, parents may rely on the administrative support and lower their own efforts.  -->

<!-- We define another family of outcomes.  -->

<!-- - Total number of applications: sum across type of the number of applications sent by either parents or administrative support -->
<!-- - Total number of applications by parents -->
<!-- - Total diversity index : sum across ECS type of dummies for at least one application in this type -->
<!-- - Parent diversity index : sum across ECS type of dummies for at least one application in this type -->


We follow the exact same strategy as the previous one although we have different hypotheses to test.

\begin{itemize}
\item
  \textbf{Hypothesis 4}: We hypothesize that information increases the total number of applications sent and we test \(\mathcal{H}_4: \hat{\beta_0}=0\) with a one sided test.

\item
\textbf{Hypothesis 5}: We hypothesize that offering information and administrative support increases the total number of applications sent. We test the null \(\mathcal{H}_5: \hat{\beta}_{1}=0\) with a one sided test of positive treatment effect of the OLS regression of equation (\ref{eq:ITTCross}).

This effect is estimated in intention to treat and simply measures the average differences between T2 and T0. We then estimate this model with covariates.


\item
  \textbf{Hypothesis 6}: We hypothesize that offering support increases the total number of applications sent compared to information only treatment. We test \(\mathcal{H}_6: \hat{\beta_2}=0\) with a one sided test.
\end{itemize}



<!-- Hypothesis 4 depends on the degree of substitution or complementarity between administrative support and parents. On the one hand, parents may rely on the administrative support to do the work and make little to no applications on their own. On the other hand, others may see this as an opportunity to increase their chances of getting a slot and exert the same effort, if not more.  -->
Like before, we estimate the effect on compliers.

Finally, we apply the same strategy in exploratory analyses over the different ECS type they parents applied to to see if treatments fosters applications to specific ECS type (see below). In particular, we expect increased access to public daycare, associative daycare, and drop-in daycare because our videos gave more details about these types of care.




\subsubsection{Treatment effects on parents' timing of application}


We define another family of outcomes to measure the timing of applications. In the endline survey, we ask parents at which date they started to apply for ECS and we have the child(ren)'s date of birth. In the baseline, we also have the month of pregnancy. 
From these, we construct a relative time measure and model the duration from the month of conception to first registration. For these outcomes, the models presented earlier do not apply. 
Instead, we use survival models to account for censoring and estimate the difference in restricted mean survival times [@NemesEtAl2020].
For the rest, we follow the same strategy as the previous outcome and we register the following hypotheses.

\begin{itemize}
\item
  \textbf{Hypothesis 7}: We hypothesize that information made parents apply earlier.
  \end{itemize}
  
  \begin{itemize}

  \item
  \textbf{Hypothesis 8}: We hypothesize that offering information and administrative support made parents apply earlier.
  \end{itemize}
  
\begin{itemize}

  \item
  \textbf{Hypothesis 9}: We hypothesize that offering support may have more positive effect on timing of application than the information-only treatment. 
  
\end{itemize}

<!-- \textbf{Hypothesis 4: Parents' timing of application}\\ -->
<!-- The intervention increases parents' likelihood to apply \textbf{early} to ECS. -->

## Final outcomes : Effects on childcare use


\subsubsection{Definition of outcomes and set of covariates}

We expect our intervention to improve to ECS access, conditional on the fact that supply-side factors are not too strong.


For this set of outcomes, we use a double-LASSO to choose vectors in $\mathbf{X}_{i}$ among baseline control variables at the parent level (mother and father level of education, employment status, country of birth, baseline level of information, household composition, intention to use ECS, past ECS use, fluency in french, number of children, coverage rate, adherence with traditional norms, amount of family and friends using ECS, access to a computer, age of the mother, whether ECS opening hours fit with parents' working hours, beliefs in ECS returns, gender of the child, level of trust in daycare centers, perceived costs, perceived opportunity costs and costs on well-being and on the career).


\subsubsection{Parents' access to ECS}   

<!--The intervention increases the likelihood that parents effectively access an ECS place.-->


Following our analysis roadmap, we first define measurement for our short-term final outcomes.
We use answers to the endline survey to define a binary variable that equals one when a person accessed to any ECS type and 0 otherwise. We will assess the veracity of parents' answers prior running these analyses.

Our baseline strategy consists in estimating equation (\ref{eq:ITTCross}) with OLS over \(\bar{Z}^2\) and \(\bar{Z}^0\) i.e.~comparing T1 and T0 and T2 and T1 to retrieve the intention to treat parameters. We index the estimations of the ITT parameters \(\beta_g\) with \(g \in \{1,2\}\), the corresponding treatment arms. Note that \(\beta_2\) is computed against parents who also received the information treatment.

-\textbf{Hypothesis 10} (subset \(\bar{Z}^2\)): We hypothesize that the information treatment increases the likelihood that parents access a place in ECS.


\begin{itemize}
\tightlist
\item
  We test the null \(\mathcal{H}_{10}: \hat{\beta_0}=0\) with a one sided test of positive treatment effect.
\end{itemize}

  
-\textbf{Hypothesis 11}(subset \(\bar{Z}^1\): We hypothesize that offering information and administrative support increases the likelihood that parents access a place in ECS.


\begin{itemize}
\tightlist
\item We test the null \(\mathcal{H}_{11}: \hat{\beta}_{1}=0\) with a one sided test of positive treatment effect of the OLS regression of equation (\ref{eq:ITTCross}).
\end{itemize}

This effect is estimated in intention to treat and simply measures the average differences between T2 and T0. We then estimate this model with covariates.


-\textbf{Hypothesis 12} (subset \(\bar{Z}^0\)): We hypothesize that offering administrative support increases the likelihood that parents access a place in ECS compared to information only.

\begin{itemize}
\tightlist
\item
  We test the null \(\mathcal{H}_{12}: \hat{\beta_2}=0\) with a one sided test of positive treatment effect.
\end{itemize}



We follow the road map and estimate these models with covariates chosen among the relevant set of variables presented above. We adjust p-value for the FWER over each pair of test (with or without covariates).

We estimate also the average treatment effect on compliers with a 2SLS of equation (\ref{eq:2SLS}).
We also test the null \(\mathcal{H}_\delta: \delta=0\) with a one sided test.

Finally, we apply the same strategy in exploratory analysis over the different ECS type they registered to see if treatments fosters access to specific ECS type. In particular, we expect increased access to public daycare, associative daycare, and drop-in daycare because our videos gave more details about these types of care.




<!--As pre-registered in the main document and according to our theory of change presented in Figure \ref{fig:ThChange}, the following hypotheses will be tested.-->

\sectionmark{Intermediate outcomes}
## Intermediate outcomes: parents level of information and perception of ECS
\sectionmark{Intermediate outcomes}

\subsubsection{Definition of outcomes and set of covariates}


We define another family of outcomes to measure how the intervention affected parents level of information about ECS. 

For this set of outcomes, we use a double-LASSO to choose vectors in $\mathbf{X}_{i}$ among baseline control variables at the parent level (mother and father level of education, employment status, country of birth, baseline level of information, household composition, intention to use ECS, past ECS use, fluency in french, number of children, coverage rate, adherence with traditional norms, amount of family and friends using ECS, access to a computer, age of the mother, whether ECS opening hours fit with parents' working hours, beliefs in ECS returns, gender of the child, level of trust in daycare centers, perceived costs, perceived opportunity costs and costs on well-being and on the career).


\subsubsection{Parents' level of information about ECS}  
Following our analysis roadmap, we first define measurement for our intermediate outcomes.
We want to know whether we increased their general level of information, and the accuracy of perceived ECS costs. Our main measurements are:

a) Number of ECS types known, 
b) Whether parents know that ECS prices vary according to resources, 
c) Parents' subjective level of information coded ex-post by the interviewers,


We will have three separated information variables on which we will estimate the effect of our interventions, testing hypotheses 13, 14 and 15. We use stacked regression and jointly estimate the effect on the three outcomes and test the null that they are all equals to 0 against at least one is positive.

We follow the exact same strategy as before although we have different hypotheses to test. For each of these variables, we make the following hypotheses:

\begin{itemize}
\item
  \textbf{Hypothesis 13}: We hypothesize that information made parents more informed about ECS and we test \(\mathcal{H}_{13}: \hat{\beta_0}=0\) with a one sided test.
  \end{itemize}
  

\begin{itemize}
\item
\textbf{Hypothesis 14}: We hypothesize that offering information and administrative support increases the likelihood that parents access a place in ECS. We test the null \(\mathcal{H}_{14}: \hat{\beta}_{1}=0\) with a one sided test of positive treatment effect of the OLS regression of equation (\ref{eq:ITTCross}).
\end{itemize}

This effect is estimated in intention to treat and simply measures the average differences between T2 and T0. 


\begin{itemize}
\tightlist
\item
  \textbf{Hypothesis 15}: We hypothesize that offering administrative support+information have more positive effect on parents' information level than information only. We test \(\mathcal{H}_{15}: \hat{\beta_2}=0\) with a one sided test.
\end{itemize}



We follow the road map and estimate these models with covariates chosen among the relevant set of variables presented above. We adjust p-value for the FWER over each pair of test (with or without covariates).

We estimate also the average treatment effect on compliers with a 2SLS of equation \ref{eq:2SLS}.
We also test the null \(\mathcal{H}_\delta: \delta=0\) with a one sided test.

\FloatBarrier
\subsection{Cross Hypotheses: Heterogeneity}

For the heterogeneity analysis, we focus only on T2, the group with highest treatment intensity that is most likely to yield large enough effect size for us to detect. We test heterogeneity in intention to treat and with instrumental variable using again the stacked-regression trick to recover the variance covariance of the error and jointly test equality between treatment effects [@OberfichtnerTauchmann2021].

a. *Social background*: We are willing to answer research question \ref{RQ1a} and research question \ref{RQ2a}. Indeed, we expect low-SES parents to benefit more from the intervention because they are more likely to misperceive the ECS offer at Baseline due to informational barriers, and to experience behavioral barriers during the application process. Our intervention eases all those constraints so we expect that they benefit from it.

High-SES may also benefit from the intervention. For example, it may be easier for high SES parents to use the information provided or take advantage from our help. However, we expect high-SES parents to navigate the system very well, even without our intervention. 
<!-- \todo[inline]{Dernière réu : Low SES on prédit une direction : pour les high SES on sait pas et c'est une question à tester. } -->
<!-- \todo[inline]{Laudine : Vraiment ? On pense vraiment qu'on va aider les high-SES ? Je dirait maybe à la marge, mais en moyenne ils s'en sortent pas très bien sans nous. Je pense qu'on peut quand même dire qu'on s'attend à aider les low SES *plus* non ??} -->

Therefore, we posit: 
 \textbf{Hypothesis 16}: We hypothesize that T2 will have a larger impact on low-SES parents. 
 To measure SES, we will use a dummy that takes the value one if the mother has attended tertiary education, and 0 otherwise. 
 
 
\paragraph*{Robustness:} we will test the robustness of these findings using alternative measurements of SES: 

i) *Occupation*: we will convert mothers' occupation in ISCO 08 classification, then we will convert ISCO 08 in ISEI (score of occupational prestige), and finally we will dichotomize this score in a dummy taking value 1 if the mother is above the median ISEI score of our sample, and 0 otherwise;  
ii) *Income*: we will create a dummy that takes the value 1 if the household is above median income of our sample and 0 otherwise; 
iii) *Activity*: we will create a dummy that takes the value 1 if the mother was employed at baseline, and 0 otherwise. 

For all these measurements, including education, we will start by taking the situation of the mother (except for income). Then, we will test alternative specifications by taking a dominance criteria: we will take the highest value of the household. For instance, if the mother has no tertiary education but the other parent does, we will code this household as having tertiary education.

b. *Past ECS usage*: 

 \textbf{Hypothesis 17}: We hypothesize that T2 will have a larger impact on parents who have never used ECS.
 
We define a dummy that take the value 1 if parents had already used ECS at baseline, and 0 otherwise. 


c. *Level of information*: We expect relatively less-informed parents at baseline to benefit more from the intervention compared to more informed ones. 
After the end of the baseline questionnaire, surveyor marked parents knowledge of ECS and we use this variable to define groups of High/low information at baseline.

 \textbf{Hypothesis 18}: We hypothesize that T2 will have a larger impact on parents who had low level of information at baseline.
 

<!-- \todo[inline]{Measure : summary index? voir plus haut. pas sur du truc. -->

<!-- dummy avec les infos des enquêtrices. -->

<!-- Sens de la relation: mediation du niveau d'info Endline. triple diff -->
<!-- Before / after Treated / untreated / Low info (baseline) / high info (baseline) -->
<!-- Low info treated effect +++ -->

<!-- Idée : instrumenter info at endline by T2 separately for high/low info at baseline pour mesurer l'effet sur l'accès. -->
<!-- $\Delta$ info baseline endline stratifie en groupe gros progrès peu progrès : effet du traitement parmi ces groupes stratifié ex post (voir Principal stratification Rubins ) -->

<!-- } -->
<!-- \todo{Laudine : Arthur tu peux faire celle là ? je pense que tu es mieux placé que moi pour écrire ce que tu avais dans la tête} -->

d. *Migration background*: 

 \textbf{Hypothesis 19}: We hypothesize that T2  will have a larger impact on foreign-born parents.
 
 Indeed, they are more likely to misperceive the ECS offer at Baseline due to informational barriers, and to experience behavioral barriers during the application process.
We will introduce an interaction term with a dummy that take the value 1 if the mother is not born in France, and 0 otherwise.


\begin{itemize}
\tightlist
\item
We test \(\mathcal{H}_{19}: \hat{\beta_1}=0\) with a one sided test.
\end{itemize}

<!-- The proximate outcome “Parents’ likelihood to apply” represents the primary outcome of this intervention. -->

## Exploratory analyses:

The effect of several additional variables will be relevant to explore:

1) *Coverage rate in ECS*: We expect the effect of our intervention to vary according to the cover rate in ECS. We will compare parents living in areas with a cover rate in ECS below the median cover rate of the sample with parents living in areas above this median cover rate.
We will introduce an interaction term with a dummy that take the value 1 if leave in an area with a below-median ECS coverage rate, and 0 otherwise. 

 We don't make any prediction about the direction of the effect. Indeed, our  intervention aims at easing process, and  make registration earlier, which is  crucial to gain priority points to get a place [@CombeHeim2023]. Therefore it  may be easier to get apply and get access to ECS in high coverage rate cities.  However, the program may also increase parents relative competitivity in highly  competitive context, that is, for instance, they apply earlier, make more  applications and navigate the ECS market more easily than non-treated parents.  Hence, it may increase their probability of getting a daycare slot in higly competitive contexts. 

2) *ECS types*: We will apply the same strategy as in our main analyses to explore the impact of our interventions on the different ECS type. We want to see if treatments fosters demand for and access to specific ECS types. In particular, we expect increased access to public daycare, associative daycare, and drop-in daycare because our videos gave more details about these types of care. We will define dummies for applications to each type of childcare. 

3) *Intention*: The baseline questionnaire collects respondents’ *intention to apply*. It will be relevant to explore if treatment impacts are larger for parents that already intended to apply before child birth, or for those that were undecided, or even for those that were opposed to ECS at baseline.

4) *Temporal preferences*: The baseline questionnaire collects respondents’ temporal preferences. Previous behavioral interventions among low-SES parents showed that information + behavioral tools (e.g., reminders) delivery have larger effects on more present-orientated parents @MayerEtAl2019. Hence, it will be relevant to explore if treatment impacts are larger for more present-orientated subjects.  

5) *Intervention to birth date timing*: @CombeHeim2023 showed that one major factor that drives ECS access inequalities among parents that applied is that high-SES parents apply very early during pregnancy. Therefore, it will be relevant to explore if the impact of treatment is larger when parents received the intervention early during pregnancy. 

6) *Single-parent families*: It will be relevant to explore the heterogeneity of the treatment effect according to whether the family is a single-parent family or not.

7) *Date of birth of the child*: As the time at which the children are born during the year is known to affect childcare arrangements , it will be relevant to explore the heterogeneity of the treatment effect according to whether the date of birth of the child.

8) *Effect on other siblings*: There may be spill-overs of the treatment on other siblings that are less than 3 years-old. It will be relevant to explore them.

9) *Beliefs in returns*: We have a measure of whether parents had high or low beliefs in ECS returns. We expect parents having high beliefs in return to benefit more from the intervention.

10) *Norms*: We measure adherence to traditional norms in the questionnaire. It will be relevant to explore the heterogeneity of the treatment effect according to adherence to traditional norms.

11) *Perception of the supply*: We measure parents perception of the supply (perceived difficulty of accessing a place, perceived fit with working hours, perceived accessibility of information about ECS). It will be relevant to explore the heterogeneity of the treatment effect according to parents' perception of the supply.


<!-- ### Submitted application to formal childcare -->

<!-- Our first research question is whether the program affects the probability of submitting applications to formal childcare.  -->

<!-- The main outcome is a parsimonious representation of parents  -->
<!-- access to any formal childcare. Formally: -->
<!-- \[ -->
<!-- R = \mathds{1}\left\{ -->
<!-- \begin{matrix} -->
<!-- \text{Public Daycare centers \& Drop-in Daycares}\quad& or \\ -->
<!-- \text{Private daycare}\quad &or \\ -->
<!-- \text{Associative daycare}\quad &or \\ -->
<!-- \text{Childminder (Assistantes maternelles)}\quad &or \\ -->
<!-- \text{nannies}\quad &or \\ -->
<!-- \text{other formal} \\ -->
<!-- \end{matrix}\right. -->
<!-- \] -->

<!-- But access to formal childcare is conditioned upon registration -->


<!-- We define a dummy variable capturing registration to any childcare mode (daycare, childminders,...). -->


<!-- \todo[inline]{Arhur qu'est ce qu'on fait avec ça ?} -->





# Data collection 
\label{sec:data}
See the "Data collection procedure" section of the main information for registration document. 

## Collected variables

### Baseline survey 

Questionnaires are administered on a tablette with the support of the interviewer. 
The following variables are collected in the questionnaires:   

-	Socio-demographic characteristics of the family (level of education; migratory background; mothers and household income; activity) 
-	Intention to use ECS (yes, no, don't know yet)      
-	Level of information on ECS (e.g., types of ECS known, perceived costs)
-	Planned activity after child delivery (i.e., whether the mother is planning to go back to work/look for a job after child delivery, and if so when)     

Some other information is also collected to understand the determinants of the application to ECS:     

-	Deprivation/salience of vital needs      
-	Temporal preferences      
-	2 measurements of mothers’ investment and health behaviors during the pregnancy i) smoking behavior during the pregnancy ii) breastfeeding intention      
-	Informal care available      
-	Social resources available (e.g., friends to help parents fill the forms)     
-	Perceived impact of staying at home on the mother’s professional career and wages    
-	Perceived impact of staying at home on the mother’s wellbeing     
-	Parents’ beliefs about children’s development: how long should a child be (exclusively) cared after by her parents; benefits of ECS on children’s development; skills one child should acquire during early childhood
-	Parents’ level of trust in several communities to take care of their children 
  
  i) parents and brothers and sisters 
  ii) the rest of the family 
  iii) Friends 
  iv) Childminders (assistante maternelle) 
  v) childcare centers (crèches)     

-	Social norms regarding childcare     
-	Access to a computer   

### Endline survey
CATI Questionnaires: questionnaires administered on the phone to participants by an interviewer assisted with a computer.
The following variables are collected in the questionnaires:

1) **Information about the baby**:   

  - Multiple pregnancy: No, Twins, Triplets, etc.
  - Prematurity: YN, number of weeks
  - Birth Date(s) of the babies
  - Assigned sex at birth of the baby
  - First Name of the baby
  - Birth Weight of the baby
  - Health outcomes: 
    
    i) whether the baby has any particular chronic health condition or disability, 
    ii) nights spent in the hospital since home return, 
    iii) subjective health
  
  - Breastfeeding: YN, length
  - Whether the family have a Family Allowance fund account (Caf) for the   baby, and if not why?
All outcomes are collected for every baby in case of multiple pregnancy

2) **Mother health and well-being**:

  - Health outcomes: night spent in the hospital at birth; nights spent in the hospital since the mother and the baby came out of the maternity hospital for the first time.
  - Well-being: we will use the french version of the WHO 5 well-being index 

3) **Treatment-related outcomes**:

  - Whether the family received the text messages with links to videos (Y/N)
  - Compliance: whether the family watched the videos (Y/N), how many (/5),  watched until the end (Y/N). If not watched, why?
  - Perceived usefulness: 0 to 10 scale
  - General satisfaction: 0 to 10 scale

4) **Situation of the household**:

  - Family composition at the time of the interview
  - Labor market outcomes: employment status and/or plans, date of return to work, full-time or part-time employment, relative intensity of labor   market situation compared to before pregnancy, and occupation.
  The questions will be asked for the two parents if the parents are still   together.
  - Housing situation: moving since baseline questionnaire (Y/N), where, and when if so.
  - Second-generation migration status

5) **Childcare related outcomes**:     
a) *ECS behavior*:  

  - ECS use (Y/N)
  - Applied to ECS (Y/N)
  - Ideal type of childcare wanted, and reason for not using the ideal childcare type if so.
  - If they have another baby less than 3yo: ECS-related outcome for this baby (see below)     
    
If the household uses ECS:      
  
  - Type of ECS used as the main childcare solution      
  - ECS use start date
  - Intensity of use: Number of hours per weeks        
  - Is the household satisfied with the current number of hours of use   (Y/N)      
  - Secondary childcare solution: does the household combine several childcare solutions? If so, type of ECS used      

If the household doesn't access ECS:

  - Current childcare solution use (e.g., maternal or paternal care, informal care)    

Then for those who applied to at least one ECS type:  

  - Type of ECS and number of applications     
  - Status of the application (in progress, rejected, or refused). Reason of refusal if so. If rejected, did they renew the application, and if   not, why?     
  - Timing of application: when did they start to apply to ECS    
  - Initial starting date wanted      
  - Application behavior: did they call ECS? Did they go on-site? Did they   use their personal or social network?       

For those who did not apply to any ECS:
- ECS plans (Y/N)       
- Did they look for information (Y/N), and if so, when?

If they plan to use ECS:     
- ECS type     
- Starting date wanted      

b) *ECS perceptions*:

- Information level: perceived cost of childcare, knows that the price is reduced through subsidies (Y/N), number of ECS known, subjective level of information (coded ex-post by the interviewer)
- Perceived ECS accessibility
- Perceived accessibility of information about ECS
- Perceived compatibility with working hours
- Perceived control over the ECS outcome: 0 to 100 scale
- Level of stress due to ECS: 0 to 100 scale
- Perceived complexity of the application process: 0 to 100 scale
- Access to informal care (as much as needed, from time to time, for emergency cases, never)
- Ideal entry age in ECS for the child
- Perceived norms: a) Perceived proportion of mothers using ECS, b) Perceived proportion of mothers opposed to ECS, c) adherence to traditional norms
- Non-monetary costs of using ECS or not: a) on well-being, b) on career, c) opportunity costs.
- Perceived beliefs in ECS returns

Questionnaires are available in 3 languages: French, English, and Arabic.


## Exclusion rules
For Baseline, see the "Targeting" section within the "Experimental Design" section of the main information for registration document.    

For Endline, the following exclusion rules will be applied:
i) If the Premiers Pas child died since Baseline interview, ii) If the parents have no Family Allowance fund account for the baby (because parents are undocumented),
iii) If the parents don't understand a simple level of French, Arabic, or English. Some participants may have gone through the inclusion process at Baseline because a translator translated the Baseline survey for them in the maternity wards, and the Research Assistant thus included them in the trial.


<!-- # Estimation methodology -->
<!-- \label{sec:Models} -->

<!-- ## Instruments -->
<!-- What data collections instruments will you employ? -->
<!-- – What (groups of) indicators will each instrument cover? -->
<!-- – How was each instrument developed? -->
<!-- – Have each instrument been used before? -->
<!-- – If so, by whom? If not, are you piloting it? -->
<!-- – What are the main advantages/disadvantages of each instrument -->


<!-- ## Dealing with outliers -->

<!-- ## Dealing with missing values -->

# Data processing and security


\begin{itemize}
\item
  \textbf{Data protection officier}: The project has been conducted with a close collaboration with Sciences Po's Data Protection Officer to ensure compliance with data protection regulations throughout the project.
\item
  \textbf{Secure Cloud Storage}: Data is securely stored on an encrypted cloud platform with very restricted access to prevent unauthorized access and data breaches. 
  \item
  \textbf{De-identification and persona information storage}: All personally identifiable information (PII) has been removed from the dataset. Any remaining identifying data is stored in a separate VeraCrypt-encrypted directory, adding an extra layer of security. 
  \item
  \textbf{Secure Cloud Storage}: Data is securely stored on an encrypted cloud platform with very restricted access to prevent unauthorized access and data breaches. 
\end{itemize}

These measures collectively safeguard data integrity and protect the privacy of individuals involved in the research.
<!-- ### Notation and parameters of interest -->

<!-- We consider a sample with $n$ units, numbered 1 through $n$ that are partitioned into $b$ blocks, numbered $1$ through $b$ -->
<!-- with each block containing $n^b$ units with $n^b\geq 3$. -->

<!-- Let $Y_i$ denote an outcome of interest, for instance  -->
<!-- $$ -->
<!-- Y_i=\left\{ -->
<!-- \begin{aligned} -->
<!-- 1 ~&\text{if parent applied to ECS}\\ -->
<!-- 0 ~&\text{otherwise} -->
<!-- \end{aligned} -->
<!-- \right. -->
<!-- $$ -->
<!-- $Z_i$ the treatment assignment status such that: -->
<!-- $$ -->
<!-- Z_i=\left\{ -->
<!-- \begin{aligned} -->
<!-- 2 ~&\text{Assigned information + assistance}\\ -->
<!-- 1 ~&\text{Assigned information}\\ -->
<!-- 0 ~&\text{Assigned Placebo} -->
<!-- \end{aligned} -->
<!-- \right. -->
<!-- $$ -->


<!-- ## Hypotheses testing -->

<!-- ```{r, echo = FALSE, message=FALSE, warning=FALSE} -->

<!-- list_Waves <- list.files("Databases",pattern = "*.csv") -->

<!-- db <- c() -->
<!-- full <- c() -->
<!-- for (file in 1:length(list_Waves)){ -->
<!--   db <-   read_csv(paste("Databases/",list_Waves[file],sep="")) %>% mutate(Wave=file) -->
<!--   assign(list_Waves[file] %>% str_remove(.,".csv"),db) -->
<!--   full <- bind_rows(full,db) -->
<!-- } -->


<!-- ``` -->



<!-- ## Balancing Checks -->

<!-- How will you check balance between treatment and control groups? -->
<!-- – What is the specification that you will run? -->
<!-- – What variables will you include in these balancing checks? -->
<!-- • How will you check balance between attritors and non-attritors? -->
<!-- 5 -->
<!-- – What is the specification that you will run? -->
<!-- – What variables will you include in these balancing checks? -->

<!-- ## Treatment effects -->

<!-- ### Intent to Treat -->
<!-- • How will you estimate the (causal) effect of the offer of the treatment? -->
<!-- – What is the specification that you will run? -->
<!-- – What controls will you include in your specification? -->

<!-- ### Treatment on the Treated -->
<!-- Same -->

<!-- ## Heterogeneous effects  -->
<!-- Replicating the above main specification separately by each of the following variables: SES, IMM, AREA, MON, SEX and MONTH. -->
<!-- SES= parental education (basic, short/long high school diploma, short/long tertiary, converted in years of education)     -->
<!-- IMM= immigration status (both/one/no parents born outside France or western countries)     -->
<!-- MON= single-parent family (Y/S)    -->
<!-- AREA = coverage rate (above or below the median)     -->
<!-- SEX= gender of the child    -->
<!-- MONTH= month of pregnancy     -->



<!-- ### Intent to Treat -->

<!-- How will you estimate the heterogeneous effects of the offer of the treatment? -->
<!-- – What are the specifications that you will run? -->
<!-- – What controls will you include in your specification? -->

<!-- ### Treatment on the Treated -->
<!-- Same -->

<!-- ## Standard Error Adjustments -->
<!--  How will you account for clustering in your data? -->
<!-- • How will you address false positives from multiple hypothesis testing? -->
<!-- – If you plan to adjust your standard errors, what adjustment procedure -->
<!-- will you use? (e.g., Family Wise Error Rate, False Discovery Rates, etc.) -->
<!-- – If you plan to aggregate multiple variables into an index, which variables -->
<!-- will you aggregate and how? -->
<!-- – How will you deal with outcomes with limited variation? -->

# Research Team
The research team is as follows:

- Laudine Carbuccia, PhD student at the Center for Research on Social Inequalities (Sciences Po) & at the Department of Cognitive Science at ENS/PSL. She works full-time on the project.       
- Arthur Heim, PhD candidate,at Paris School of Economics and research and evaluation officer at the National family allowance fund (Cnaf)  
<!-- \todo[inline]{Laudine: rappel à Arthur de mentionner la Cnaf} -->
- Carlo Barone, full professor of Sociology at the Center for Research on Social Inequalities (Sciences Po).  
- Coralie Chevallier, cognitive psychologist at the Department of Cognitive Science at ENS/PSL.   

<!-- # Calendar -->
<!-- - September to December 2022: Recruitment and Baseline survey. -->
<!-- - October to December 2022: Randomization and Informational Treatment. -->
<!-- - February to June 2023: Administrative support for participants from the second experimental group. -->
<!-- - October 16th to December2023: Endline survey -->

<!-- A follow-up assessing the impact on parents' labor market outcomes and children development would be done approximately one year after the endline. -->

<!-- # Ethics information -->
<!-- The study was approved by the international review board of Paris School of Economics (IRB number: 2022-015).  -->
<!-- All participants are given an information flyer on their rights before participating in the study. We give then a compensation for their participation. -->


<!-- # Significance-level correction -->

<!-- # Displacement effects -->

\newpage
# Bibliography
::: {#refs}
:::