# Optimal Treatment Allocation under Constraints††thanks: Acknowledgements: We
thank Nadja van ’t Hoff, Miriam Wüst, Lise Geisler Bjerregaard, Christian
Møller Dahl, Andreas Bjerre-Nielsen, and seminar participants at University of
Southern Denmark for helpful comments; Katrine Lindholm Nicolaisen for
discussions on network flows; Christian Møller Dahl for his work on image
segmentation; and Toru Kitagawa and Michael Lechner for discussions on optimal
policy. We gratefully acknowledge financial support from the Independent
Research Fund Denmark (8106-00003B). In this project, we transcribe and use
data from the “Copenhagen Infant Health Nurse Records” that was established by
the Center for Clinical Research and Prevention, the Capital Region of
Denmark, the University of Copenhagen, and the University of Southern Denmark.
We thank Thorkild I.A. Sørensen for his contributions to the establishment of
the CIHNR.

Torben S. D. Johansen Department of Economics, University of Southern Denmark,
Denmark<EMAIL_ADDRESS>
(April 2024)

###### Abstract

In optimal policy problems where treatment effects vary at the individual
level, optimally allocating treatments to recipients is complex even when
potential outcomes are known. We present an algorithm for multi-arm treatment
allocation problems that is guaranteed to find the optimal allocation in
strongly polynomial time, and which is able to handle arbitrary potential
outcomes as well as constraints on treatment requirement and capacity.
Further, starting from an arbitrary allocation, we show how to optimally re-
allocate treatments in a Pareto-improving manner. To showcase our results, we
use data from Danish nurse home visiting for infants. We estimate nurse
specific treatment effects for children born 1959-1967 in Copenhagen,
comparing nurses against each other. We exploit random assignment of newborn
children to nurses within a district to obtain causal estimates of nurse-
specific treatment effects using causal machine learning. Using these
estimates, and treating the Danish nurse home visiting program as a case of an
optimal treatment allocation problem (where a treatment is a nurse), we
document room for significant productivity improvements by optimally re-
allocating nurses to children. Our estimates suggest that optimal allocation
of nurses to children could have improved average yearly earnings by USD 1,815
and length of education by around two months.

##  1 Introduction

Across a number of settings decision makers wish to make informed choices
regarding provision of treatments to recipients in a way that maximizes some
score.111Our use of treatment is broad and may include medical treatments,
adverting, provision of services such as education, and more. Likewise, our
use of recipient is broad and may include patients, customers, students, and
more. Examples include [77, 32, 91, 7, 97, 53, 106, 19, 13, 48, 21, 24, 20],
ranging from healthcare to digital advertising and public policies. A common
theme across these settings is heterogeneous treatment effects,222For example:
Given two patients, one might respond better to drug A while the other
responds better to drug B. in turn leading to benefits from “personalized
treatment”.333This is also known as “personalized medicine” [71, 63, 93], and
can be seen as a subset of the broader setting of personalized treatment, by
which is meant a broader definition of treatments than exclusively medical
treatments. However, to exploit this information requires insight into
(estimates of) potential outcomes of recipients under different treatments and
a policy mapping that, based on potential outcomes, is able to optimally
allocate treatments to recipients, potentially while respecting constraints
related to recipient treatment rights, treatment capacities, and equity
concerns.

In this paper, we tackle the issue of optimally allocating treatments to
recipients under constraints. Related to our work is the literature on policy
learning [44, 103, 105, 104, 96, 107, 74, 78, 9, 108]. While most of the
existing literature focuses on binary treatments, exceptions include [96, 107,
73, 108]. What sets this study apart, however, is our focus on optimal
treatment allocation, and we attempt to solve the computational challenges
related to optimal policy design given potential outcomes that arise due to
large numbers of treatments and recipients and various constraints related to
treatment allocation. As such, our contribution is in developing a general
method for finding policies that exactly maximize some objective function
within a class of policies.444Or minimize some objective function, depending
on whether a larger value signifies a better outcome. Thus, our work is
related to the task of finding the policy that exactly minimizes the
approximate value function within the class of tree-based policies discussed
in [108], but where [108] use a general mixed integer program (MIP) which
quickly becomes computationally infeasible, our approach, based on a graph
representation of the problem, is more suitable for larger problems.555Recall
we abstract from any complications related to forming an approximate value
function using estimators, and thus our objective is exclusively related to
finding the optimal policy given a value function. [108] consider the more
general task of multi-action policy learning with observational data. Our
contribution could help with certain aspect of this problem but is not an
alternative to the full task.

Our contribution is in proving that the general case of optimally allocating
treatments to recipients taken potential outcomes as given is strongly
polynomial, even when (1) treatment effects are allowed to vary arbitrarily
between recipients, (2) there are arbitrarily many distinct types of
treatments available, and (3) each treatment must respect capacity
constraints. In an extension, we show that our results apply also when only
Pareto-improvements are allowed, i.e., in settings where a re-allocation of
treatments is not allowed to make any individual worse off.666Our approach
lends itself well to extensions such as differential capacities by treatment
and respecting constraints related to certain types of treatments not being
eligible for some recipients. For our proofs, we represent the optimal
treatment allocation problem as a flow problem in an appropriately constructed
network.777See the textbooks by [51, 3, 14] for introductions to flows in
networks. In addition to proving our complexity results, this representation
also lends itself well to the construction of an algorithm for solving the
problem.

To showcase our method, we consider nurse home visiting (NHV) in Denmark,
where we consider each individual nurse a treatment and each child a
recipient. NHV for infants started in 1937 in Denmark, and previous work has
documented large, positive impacts of NHV and center care in Denmark [102, 67]
as well as in Norway [31], Sweden [26], and the US [68]. We combine a rich
dataset consisting of nurse journals following infants during their first year
of life with Danish administrative data, providing information on education
and labor market outcomes.888In joint, concurrent work, [12, 28] have
transcribed the contents of the nurse records using machine learning, based
mostly on manual transcriptions from [6, 27]. The nurse journals originate
from the Danish NHV program and cover all children born between 1959-1967 and
living in Copenhagen during their first year of life. They contain information
on birth characteristics (including birth weight, birth length, and preterm
status), detailed data from visits taking place at child age two weeks and
one, two, three, four, six, nine, and 12 months (including weight development,
nutrition, and home and parent characteristics), and, crucially for this
study, the name of the nurse performing the visits for each child. Linking the
journals to Danish administrative data, we can follow the development of these
children until around age 50-60 (depending on cohort and register), from which
we obtain information on education and labor market outcomes.

The NHV setting lends itself well to our proposed method: First, using causal
machine learning combined with detailed pre-treatment data for each child and
her family, following children throughout their lives using Danish register
data, and exploiting quasi-random allocation of nurses to children within
nurse districts (and years), we can obtain individual-level treatment effects
for all children of the Copenhagen NHV program, in turn allowing us to obtain
estimates of potential outcomes under different treatments at the individual
level. Second, the setting is complex in that there are large numbers of
distinct treatments and recipients, each treatment is capacity-constrained
(for example, allocating all children to the same nurse is not a valid
solution), each recipient must be treated by exactly one treatment (exactly
one nurse allocated each child), and we may want to impose Pareto-improvement
constraints to make sure a re-allocation does not leave any child worse
off.999Or even that some children must not be left worse off, e.g., those from
families at the bottom of the socioeconomic distribution.

We start by documenting that while the initial conditions of children (as
measured by at-birth characteristics, such as birth weight, and parent
characteristics) vary significantly between nurses, this is largely driven by
differences between nurse districts as well as birth years. Once we remove
these effects, differences in pre-treatment variables are much less
pronounced, supporting our identification strategy relying on quasi-random
allocation of nurses to children within district-by-year groups. However,
clear differences in outcomes remain between children to whom different nurses
were allocated. This suggests that nurses vary in terms of their treatment
effects.101010We also directly estimate differences in nurse treatment
effects, results which are of independent interest. As we show later, the
average (absolute) difference (beyond that which can occur due to noise) in
length of education between groups of children for two separate nurses is
around one month and in average income during ages 25-50 about 1.4%.

We next turn to measuring child-specific treatment effects for each nurse.
Here, we once again exploit the quasi-random allocation of nurses to children
within district-by-year groups, and now estimate heterogeneous treatment
effects using causal machine learning while exploiting our information on pre-
treatment child and family characteristics.111111Specifically, we use multi-
arm causal forest [99, 8, 86] combined with child and family characteristics
from the nurse records transcribed using machine learning, as well as
information obtained from Danish registers by linking the transcribed nurse
records to the registers. This allows us to obtain estimates of potential
outcomes under different treatments, and using these we are able to estimate
counterfactual distributions of child outcomes under different treatment
allocation policy rules. Using our method for finding optimal policy rules, we
are able to estimate the maximum benefit from re-allocating nurses in a more
efficient manner, as well as able to estimate the share of total theoretical
benefits from re-allocation attained through other policy rules. Our estimates
suggest that optimal allocation of nurses to children could have improved
average yearly earnings by USD 1,815 (4%) and total length of education by
around two months.

We contribute to two broad strands of literature. First, we contribute to the
literature on optimal policy learning [82, 65, 44, 103, 105, 104, 66, 9, 108],
specifically on the problem of finding optimal policies taken potential
outcomes as given. Finding optimal policies is important in the sense of
optimally allocating resources and thus achieving full efficiency, but the
complex allocation mechanism to achieve this might not always be desirable;
however, even in cases where simpler allocation mechanisms are desired,
comparing such mechanisms with optimal rules has the benefit of allowing
policy makers to correctly weigh the benefits of simplicity against its costs
in terms of efficiency losses. In doing so, we also showcase how results from
graph theory, and specifically network flows [50, 51, 85, 3, 42], are helpful
in solving complex economic problems in settings where these can be
represented by appropriately constructed graphs.

Second, we contribute to the literature on the impact of early-life policies,
and in particular the role of treatment providers. The role of early-life
circumstances on short- and long-run outcomes of individuals has long been an
active area of research across disciplines, including economics [52, 4].
Within the realm of research investigating the enduring significance of early-
life health policies, two primary currents emerge:121212In addition to studies
on the positive role of early-life investments, other studies have
investigated the negative effects of early-life shocks, such as extreme
weather events, and their interactions with early-life investments policies
[1, 45, 55, 2]. The first strand consists of randomized trials that implement
high-intensity targeted model programs such as the U.S. Nurse Family
Partnership and the Perry Preschool Program, interventions which have
underscored the substantial and lasting dividends reaped from precisely
targeted investments in the well-being and development of socioeconomically
disadvantaged children [88, 89, 90, 22, 64]. The second strand exploits
naturally occurring variations in access to early-life health policies, and
noteworthy examples include diverse interventions such as nutritional and
income support programs [69, 15, 11, 17], healthcare insurance and services
[100, 62, 83, 87, 46], early educational initiatives [92, 10, 5], as well as
infant home visiting and center-based care [67, 26, 31, 68].131313In
concurrent work, [12] combine some of the strengths of these two strands by
evaluating a large-scale government trial of NHV in Copenhagen during the
1960s that quasi-randomly allocated some children to three vs. one year of
NHV. This combines individual-level data on early-life circumstances with
long-run administrative data on outcomes. Where we depart from much of this
existing literature is on our focus on the role of treatment providers, rather
than the effect of a program. Understanding the role of providers is likely a
key element in improving our understanding of optimal design and targeting of
such programs, and we contribute with novel evidence on the magnitude of
between-provider treatment effects and heterogeneity with respect to child
characteristics. Key to facilitating our application is the development and
use of machine learning (ML) for handwritten text recognition, which we use to
transcribe the handwritten nurse records and link those with administrative
data.141414In concurrent work, [28, 12] transcribe handwritten nurse records
from the 1960s Copenhagen NHV program and link those to Danish administrative
data to construct a large cohort of children (92,902) to track from birth
throughout their life. [12] use this data to study the impact of extended NHV,
exploiting a 1960s trial that quasi-randomly allocated children to three vs.
one year of NHV. This cohort also forms the population of children we use for
our application. In doing so, we also contribute to the literature on layout
detection [33, 94, 35, 38] and scene, optical character, and handwritten text
recognition [61, 30, 81, 29, 18, 56, 75, 37, 36].

The paper proceeds as follows: In Section 2, we derive our allocation
algorithm for solving the optimal allocation problem. Section 3 then presents
the institutional background of the 1960s Copenhagen infant NHV program and
Section 4 presents our data. Section 5 describes our approach for estimation
and Section 6 presents our results. Section 7 concludes.

##  2 Optimal Allocation

We define the optimal allocation problem as the problem of optimally
allocating treatments to recipients (where a number of treatments are
available), under constraints regarding recipients (receive exactly one
treatment) and treatments (at most $m$ recipients can receive given
treatment).151515This encompasses the nurse allocation problem discussed in
the paper, but it is not specific to it and may encompass a host of other such
types of problems. It is straightforward to extend the problem to settings
where capacities vary by treatments. Formally, we define the problem as:

######  Definition 2.1 (Optimal allocation problem).

Let $Y_{i}^{j}\in\mathbb{R}$ denote the outcome of recipient $i$ under
treatment $j$ and let $D_{i}^{j}\in\\{0,1\\}$ be one if recipient $i$ receives
treatment $j$. The optimal allocation problem is then the problem of choosing
$D_{i}^{j}$ such that the maximum average realized outcome is achieved, while
respecting that each recipient must be allocated exactly one treatment and no
treatment is allocated to more individuals than its capacity allows.

Noting that $D_{i}^{j}\in\\{0,1\\}$ is $1$ if individual $i$ is under
treatment $j$ and $0$ otherwise, we see that assignment of everyone to exactly
one treatment ($\sum_{j}D_{i}^{j}=1$) and respecting capacities
($\sum_{i}D_{i}^{j}\leq m$) leads to a binary program:161616If capacities of
different treatments vary, we may instead write $\sum_{i}D_{i}^{j}\leq m_{j}$
as the second set of conditions. Otherwise the problem remains unchanged.

$\displaystyle\underset{D^{j}_{i}}{\arg\max}$
$\displaystyle\,\sum_{i}\sum_{j}Y^{j}_{i}D^{j}_{i}$ such that
$\displaystyle\sum_{j}D_{i}^{j}=1\,\,\,\forall\,i\in\\{1,\dots,n\\}$
$\displaystyle\sum_{i}D_{i}^{j}\leq m\,\,\,\forall\,j\in\\{1,\dots,k\\},$

where $n$ is the number of recipients, $k$ the number of treatments, and $m$
the “capacity” of each treatment, i.e., the maximum number of recipients a
given treatment may be allocated to. The solution to this binary program is
exactly the optimal solution to the allocation problem of Definition 2.1.

We claim there exists a strongly polynomial algorithm for solving the
allocation problem (despite its potential $\mathcal{NP}$-completeness given
its structure as a binary program). For our proof, we shall make use of flows
in networks by appropriately constructing a network and representing the
optimal allocation problem as an integer minimum cost feasible flow-problem in
the constructed network.171717See the textbooks by [51, 3, 14] for
introductions to flows in networks.

Let $V_{1}$ be the set of treatments and $V_{2}$ the set of recipients, and
let $s$ and $t$ be special vertices. Define now $V:=V_{1}\cup
V_{2}\cup\\{s,t\\}$ as the set of vertices of a digraph and let
$A:=\\{sv_{1}\,:\,v_{1}\in V_{1}\\}\cup\\{v_{1}v_{2}\,:\,v_{1}\in
V_{1},v_{2}\in V_{2}\\}\cup\\{v_{2}t\,:\,v_{2}\in V_{2}\\}$ be the arcs of the
digraph, i.e., $D=(V,A)$. Define now the network $\mathcal{N}:=(V,A,l,u,b,c)$,
where $b:V\rightarrow\mathbb{R}$ is a function on the vertices and
$l:A\rightarrow\mathbb{R}$, $u:A\rightarrow\mathbb{R}$, and
$c:A\rightarrow\mathbb{R}$ are functions on the arcs. By appropriately
choosing $b$ and $l$, $u$, and $c$, it turns out that an integer minimum cost
feasible flow in the network exactly corresponds to the optimal solution of
the allocation problem. Formally, we define the network as:

######  Definition 2.2 (Network representation).

Let $\mathcal{N}:=(V,A,l,u,b,c)$ be defined as above and let, for all
$v_{1}\in V_{1}$ and $v_{2}\in V_{2}$, $l_{v_{1}v_{2}}=0$, $u_{v_{1}v_{2}}=1$,
and $c_{v_{1}v_{2}}=-Y_{v_{2}}^{v_{1}}$.181818In some algorithmic settings
non-negative costs are desired. This is easily guaranteed by adding
$\max\\{Y_{i}^{j}\\}$ to all costs (leaving the problem unchanged). We refrain
from this for notational simplicity. Further, let, for all $v_{1}\in V_{1}$,
$l_{sv_{1}}=0$, $u_{sv_{1}}=m$, and $c_{sv_{1}}=0$ and let, for all $v_{2}\in
V_{2}$, $l_{v_{2}t}=1$, $u_{v_{2}t}=1$, and $c_{v_{2}t}=0$. Finally, let
$b(v)=0$ for all $v\in V\setminus\\{s,t\\}$ and $b(s)=-b(t)$.191919This, in
turn, implies that $\sum_{v\in V}b(v)=0$. We shall call the network
constructed this way the network representation of an instance of the optimal
allocation problem of Definition 2.1.

A flow in a network is a function on the arcs $x:A\rightarrow\mathbb{R}_{+}$,
and we call it an integer flow if $x:A\rightarrow\mathbb{N}_{0}$. For a given
flow, the balance vector of $x$ is

$\displaystyle b_{x}(v)=\sum_{vw\in A}x_{vw}-\sum_{uv\in
A}x_{uv}\quad\forall\,v\in V$

We say a flow $x$ is feasible if, for all $uw\in A$, $l_{uw}\leq x_{uw}\leq
u_{uw}$ and, for all $v\in V$, $b(v)=b_{x}(v)$. Further, we define the cost of
a flow as $\sum_{uw\in A}c_{uw}x_{uw}$. We are now in a position to prove the
correspondence between the optimal allocation problem (Definition 2.1) and its
network representation (Definition 2.2).

######  Theorem 2.3.

Any integer feasible flow $x$ in $\mathcal{N}$ defined as in Definition 2.2
corresponds to a valid solution to the treatment allocation problem defined as
in Definition 2.1. Further, the cost of any feasible flow $x$ is exactly the
negative value of its corresponding value in the treatment allocation problem.

###### Proof.

We sketch the main points of the proof here. Appendix A provides further
details.

Any integer feasible flow $x$ in $\mathcal{N}$ makes use of at most $m$ arcs
from each $v_{1}\in V_{1}$ (i.e., respects capacities) and exactly one arc
from each $v_{2}\in V_{2}$ (i.e., allocates exactly one treatment to each
recipient). Let $D_{v_{2}}^{v_{1}}=x_{v_{1}v_{2}}$ for all $v_{1}\in V_{1}$
and $v_{2}\in V_{2}$. Then the set of $D_{v_{2}}^{v_{1}}$s satisfies the
constraints of the binary program formulation of Definition 2.1 and is thus a
valid solution to the allocation problem, with cost $\sum_{uw\in
A}c_{uw}x_{uw}=-\sum_{v_{2}\in V_{2}}\sum_{v_{1}\in
V_{1}}Y_{v_{2}}^{v_{1}}D_{v_{2}}^{v_{1}}$. ∎

It follows straightforwardly that the allocation problem has a solution if and
only if an integer feasible flow exists in its network representation.
Further, any integer minimum cost feasible flow in an allocation problem’s
corresponding network representation corresponds to the optimal value of the
allocation problem.

######  Corollary 2.4.

The allocation problem as defined in Definition 2.1 has a solution if and only
if $m|V_{1}|\geq|V_{2}|$, and any integer minimum cost feasible flow in its
network representation (Definition 2.2) corresponds to an optimal solution of
the associated allocation problem.

###### Proof.

Clearly, $\sum_{j}D_{i}^{j}=1\implies\sum_{i}\sum_{j}D_{i}^{j}=|V_{2}|$ and
$\sum_{i}D_{i}^{j}\leq m\implies\sum_{i}\sum_{j}D_{i}^{j}\leq m|V_{1}|$.
Hence, $m|V_{1}|\geq|V_{2}|$.

Since, by Theorem 2.3, the cost of any integer feasible flow in the network
representation of the allocation problem is equal to the negative value of the
optimal solution to the allocation problem, finding an integer minimum cost
feasible flow in the allocation problem’s network representation corresponds
to finding an optimal solution to the allocation problem. ∎

To prove that a strongly polynomial algorithm for solving the optimal
allocation problem exists, it suffices to show that an integer minimum cost
feasible flow in its corresponding network can be found in strongly polynomial
time.202020It also requires that the network representation of an allocation
problem can be found in strongly polynomial time, but this may be easily
verified.

######  Theorem 2.5.

Let $\mathcal{N}:=(V,A,l,u,b,c)$ denote the network representation (Definition
2.2) of the allocation problem (Definition 2.1) and let $n_{1}$ denote the
number of treatments and $n_{2}$ the number of recipients. Given the existence
of an integer feasible flow in $\mathcal{N}$, an integer minimum cost feasible
flow $x$ in $\mathcal{N}$ (and, in turn, an optimal solution to the allocation
problem) can be found in time
$\mathcal{O}\left[(n_{1}^{3}n_{2}^{2}+n_{1}^{2}n_{2}^{3})\log^{2}(n_{1}+n_{2})\right]$.

###### Proof.

We sketch the main points of the proof here. Appendix A provides further
details.

Let $n=|V|$ denote the number of vertices and $m=|A|$ the number of arcs in
the underlying digraph $D$ of $\mathcal{N}$. Noting that capacities (and lower
bounds and balance vectors) are integers, using the cancel-and-tighten
algorithm of [60] allows us to find a minimum cost feasible flow in
$\mathcal{N}$ in time $\mathcal{O}(nm^{2}(\log n)^{2})$ (even when costs are
arbitrary real-valued).

Noting that the cancel-and-cut algorithm is a variant of the cycle cancelling
algorithm [79], we may use a convenient integrality property of minimum cost
flows, namely that given all integer lower bounds, capacities, and balance
vectors, there exists an integer minimum cost flow: At each iteration, we
augment our flow along the cycle $C$ by $\delta(C)$, by which we mean the
minimum residual capacity of any arc on $C$ in $\mathcal{N}$, and thus our new
flow after any iteration is $x^{t+1}=x^{t}\oplus\delta(C)$. Since the residual
capacity on any arc is always an integer, $x^{t+1}$ is an integer flow so long
as $x^{t}$ is, and thus by induction we have an integer minimum cost flow.

Noting that $n=2+n_{1}+n_{2}$ and $m=n_{1}+n_{2}+n_{1}n_{2}$, we have
$\mathcal{O}(nm^{2}(\log
n)^{2})=\mathcal{O}\left[(n_{1}^{3}n_{2}^{2}+n_{1}^{2}n_{2}^{3})\log^{2}(n_{1}+n_{2})\right]$.
∎

For our application of allocating nurses to infants, our ultimate goal is to
provide guidance for a re-allocation of nurses in such a way as to maximize
their “treatment effects”. In cases where nurses differentially affect
children, i.e., there exists $i_{1},i_{2},j_{1},j_{2},i_{1}\neq
i_{2},j_{1}\neq j_{2}$ such that
$Y_{i_{2}}^{j_{1}}-Y_{i_{1}}^{j_{1}}>Y_{i_{1}}^{j_{2}}-Y_{i_{2}}^{j_{2}}$, re-
allocating nurse $j_{1}$ from child $i_{2}$ to $i_{1}$ (and nurse $j_{2}$ from
child $i_{1}$ to $i_{2}$) will improve average outcomes.212121However, there
is no guarantee that neither child is made worse off, an issue we turn to in
Section 2.1. While we do not observe all $Y_{i}^{j}$, we may use sample
estimates of these, as may be obtained by estimating heterogeneous nurse
treatment effects by child pre-treatment characteristics. Thus, our approach
is designed to solve allocation problems once (estimates of) potential
outcomes are obtained, and is then guaranteed to always be able to find the
(non-parametric) optimal allocation of treatments to recipients in strongly
polynomial time.

In a setting such as the one above, the number of treatments is required to
grow as the number of recipients does, but this might not be the case if
treatment is, e.g., a drug or an advertisement campaign. In such cases we
obtain complexity $\mathcal{O}\left[n_{2}^{3}(\log n_{2})^{2}\right]$.

###  2.1 Pareto-Improvement Guarantees

While our approach taken thus far does not guarantee that no child is made
worse off, it is easily extendable to cover scenarios where only Pareto
improvements are allowed. Given some “initial solution” (allocation of
treatments to recipients), we call this new problem the Pareto-guaranteed
optimal allocation problem and formally define it as:

######  Definition 2.6 (Pareto-guaranteed optimal allocation problem).

Let $Y_{i}^{j}\in\mathbb{R}$ denote the outcome of recipient $i$ under
treatment $j$ and let $D_{i}^{j}\in\\{0,1\\}$ be one if recipient $i$ receives
treatment $j$. The Pareto-guaranteed optimal allocation problem is then the
problem of choosing $D_{i}^{j}$ such that the maximum average realized outcome
is achieved, while respecting that each recipient must be allocated exactly
one treatment, that no treatment is allocated to more individuals than its
capacity allows, and that no re-allocation leads to any recipient be made
worse off compared to the baseline choices of $D_{i}^{j}$.

We shall make use of a slight modification to the network representation of
Definition 2.2 to prove our extension:

######  Definition 2.7 (Pareto-guaranteed network representation).

Let $\mathcal{N}:=(V,A,l,u,b,c)$ be defined as in Definition 2.2. Remove arcs
from $\mathcal{N}$ as follows: For each recipient $v_{2}^{*}\in V_{2}$, let
$\bar{Y}_{v_{2}^{*}}^{v_{1}^{*}}$ denote the realized outcome under no re-
allocation, i.e., nurse $v_{1}^{*}$ is allocated $v_{2}^{*}$ under no re-
allocation. Now, for each $v_{1}\in V_{1}$ and $v_{2}\in V_{2}$, remove the
arc $v_{1}v_{2}$ if $Y_{v_{2}}^{v_{1}}<\bar{Y}_{v_{2}^{*}}^{v_{1}^{*}}$ to
construct the network $\mathcal{N}_{P}$.222222Alternatively, one could set
$u_{v_{1}v_{2}}=0$ in these cases. We shall call $\mathcal{N}_{P}$ constructed
this way the Pareto-guaranteed network representation of an instance of the
Pareto-guaranteed optimal allocation problem of Definition 2.6.

With our modified network definition, we are in a position to prove that our
results extend to settings where only Pareto improvements are allowed.

######  Theorem 2.8.

Let $\mathcal{N_{P}}$ as defined in Definition 2.7 be the Pareto-guaranteed
network representation of the Pareto-guaranteed optimal allocation problem of
Definition 2.6, and let $n_{1}$ denote the number of treatments and $n_{2}$
the number of recipients. Given the existence of an integer feasible flow in
$\mathcal{N_{P}}$, an integer minimum cost feasible flow $x$ in
$\mathcal{N_{P}}$ is guaranteed to make no recipient worse off and to
correspond to the (non-parametric) optimal allocation given the constraints.
The solution can always be found in at most time
$\mathcal{O}\left[(n_{1}^{3}n_{2}^{2}+n_{1}^{2}n_{2}^{3})\log^{2}(n_{1}+n_{2})\right]$.

###### Proof.

Under the constraints of Definition 2.6, no flow $x$ with value more than $0$
may pass through one of the arcs deleted when modifying $\mathcal{N}$ to
$\mathcal{N}_{P}$. Thus, we may without loss of generality remove these arcs.
The correspondence of an integer minimum cost feasible flow in
$\mathcal{N}_{P}$ and the optimal solution to the Pareto-guaranteed optimal
allocation problem then follows from Theorem 2.3.

Using Theorem 2.5 (which puts no restriction on $\mathcal{N}$), we can always
find an integer minimum cost feasible flow (if one exists) $x$ in
$\mathcal{N}_{P}$ in at most time
$\mathcal{O}\left[(n_{1}^{3}n_{2}^{2}+n_{1}^{2}n_{2}^{3})\log^{2}(n_{1}+n_{2})\right]$.
∎

Generally, our approach for solving the optimal allocation problem is readily
generalizable to a broad range of alternative settings. In fact, any
alternative formulation of the problem which can be represented by the type of
network we introduce is immediately covered (with one such example being the
Pareto-guaranteed optimal allocation problem). Other settings include the
possibility of multiple (additive in effect) treatments available for some
recipients (by appropriately changing capacities of the type $u_{v_{2}t}$) and
treatments being differentially available to recipients (by appropriately
removing arcs of the type $v_{1}v_{2}$).

##  3 Institutional Background of the 1960s Copenhagen Nurse Home Visiting
Program

In this section, we give an overview of the 1960s Copenhagen NHV program that
serves as the background of our empirical application of the results derived
in Section 2. The 1960s Copenhagen NHV program provides the scene for the
study by [12] on the role of extended NHV, and we refer the interested reader
to that paper for additional details on the program, and in particular the
Copenhagen trial on extended NHV.232323The cohort profile we have created as
part of our efforts of transcribing and linking the NHV records is described
in more detail in [28].

Universal home visiting for families with infants in Denmark has a rich
history, dating back to 1937 when the Danish National Board of Health (DNBH)
launched a program to address high infant mortality rates. This initiative
aimed to combat infant mortality rates of around six percent in the early
1930s. Utilizing staggered introductions across municipalities from 1937 to
1949, previous research has highlighted both short- and long-term health
benefits of program participation [102, 67].

By the 1960s, with significant improvements in living conditions and a decline
in infant mortality rates to around two percent, the DNBH revised the program
to emphasize broader health monitoring and encourage relevant parental health
investments [41]. This shift in focus aligns with the evolving landscape of
early childhood programs, such as the US Head Start program, which also
underscored parental investments during toddler years [16]. With midwife-
assisted home births being the norm and limited formal childcare options,
interventions in the family home, especially during toddler years, gained
prominence.

Amid these developments, the DNBH conducted experiments with extended home
visiting, including the “Copenhagen trial” studied by [12], which encompassed
children born between 1959 and 1967.242424Exploiting quasi-random allocation
to a three (vs. baseline one) year NHV program in Copenhagen in the 1960s,
[12] document positive long-run health (and to a lesser extend employment)
effects, and notably significant heterogeneity with respect to characteristics
such as birth weight (with low birth weight children much more positively
affected than the average child). In this trial, nurses offered additional
follow-up during existing first-year visits to families residing in
Copenhagen. While the “Copenhagen trial” aimed at evaluating the efficacy of a
longer visiting schedule, it also meticulously tracked child development
during the baseline period (that is, the first year of a child’s life) for
everyone living in Copenhagen and born between 1959-1967. Table 1 shows an
overview of topics covered at different visits during a child’s first year
visits.252525The position as an infant health nurse required education beyond
that of an ordinary nurse, within maternity care, specialized paediatric care,
epidemic or tuberculosis care, or care for patients with mental illness. All
infant health nurses had to pass a course at Aarhus University [70, 39, 40].
Topics include objective development measurements (e.g., child weight), self-
reported parenting decisions (e.g., type of nutrition), and nurse-assessed
family characteristics (e.g., socioeconomic status and mother well-
being).262626While more than the eight visits indicated in Table 1 could take
place (with an average of 13 visits per child taking place), structured
information collection took place at these eight visits, with the nurse
records containing pre-printed fields to be filled in at these specific
visits.

Table 1: Content of the First Year Home Visiting Program in Copenhagen.

|  | Age of Child
---|---|---
Topic |  Example Items | 2 weeks | 1, 2, 3, 4, 6, 9 months | 12 months
Family |  Socioeconomic status, mother mental and physical health |  | ✓ | ✓
Mother labor force |  Employment status, childcare status |  | ✓ | ✓
Nutrition |  |  |  |
a. |  Infant feeding, number of meals | ✓ | ✓ | ✓
b. |  Duration of breastfeeding |  |  | ✓
Child development |  |  |  |
a. |  Smiles, lifts head, babbles, sits alone |  | ✓ | ✓
b. |  Height |  |  | ✓
c. |  Weight | ✓ | ✓ | ✓
d. |  Walks, #teeth, general health assessment, vaccination status, ever hospitalized |  |  | ✓
Child sleeping conditions |  Own bed |  | ✓ | ✓

Notes: The table shows topics covered in the first-year visits and example
items for nurse registrations in the children’s records. At each age, more
than one nurse visit could be performed (depending on family needs), with an
average of around 13 first year visits during the trial ([34], various years).
For each age-specific topic, nurse registrations were made at one of those
visits. Source: Table due to [12].

While the “Copenhagen trial” altered the landscape of child home visiting, it
did so in a way unlikely to contaminate the study of differences in the impact
of NHV by nurse, namely by quasi-random allocation to the prolonged program by
day of the month of birth, assigning everyone born the first three days of any
of the months of the nine year trial to the extended schedule. While the
number of visits each child received was reduced as a consequence, in order to
compensate nurses for the additional visits to the children enrolled into the
extended schedule,272727The average number of first year visits was reduced to
around 13, compared to the pre-trial average of around 14 ([34], various
years). this was done in a “homogeneous” way across children and should not
interfere with our design.

##  4 Data

Our study combines two primary sources of data, those being handwritten nurse
records from the 1960s and Danish administrative data, to allow us to combine
detailed information on childhood development with long-run outcomes from
administrative register data, in total following individuals from their birth
to when they are around 50-60 years old (depending on their year of birth).
Additionally, we use archive material detailing which nurse district each
nurse of the Copenhagen infant nurse program worked in. Combining these
sources, we are able to identify which nurse visited each child and follow
that child throughout her first year of life and from her adulthood until
current time.

###  4.1 Copenhagen Nurse Records

Nurse records with information on childhood development is available for all
children born in Copenhagen between 1959-1967.282828Years before or after are
not available, and we speculate that these years were archived due to those
being the years of the “Copenhagen trial” studied in [12]. Figure 1 shows the
scan of a nurse journal of a child, with parts blackened for confidentially
reasons (in the source material we have available, these black patches are not
present).

Figure 1: Sample Nurse Record for a Copenhagen Child.

Notes: The pages depict a scanned nurse record of a child. For confidentiality
reasons, parts of the pages are blackened. The first page contains the table
for first-year nurse registrations. The second page (flip side) is a page
primarily for nurse comments in free text. The third page contains the table
for second- and third-year registrations (the “treatment table”). The final
page (flip side) allows for further nurse comments during the second and third
year. Source: Figure due to [12].

In joint, concurrent work, [12, 28] use ML to transcribe the contents of these
records and link them to Danish administrative register data.292929See [35]
for details on an unsupervised ML approach we use to identify types of journal
pages and, as a consequence, identify which children were part of the
treatment arm of the “Copenhagen trial”. While the Danish unique personal
identifier was introduced in 1968 – i.e., after the birth of all the children
of the records – we nevertheless are able to obtain their personal
identification number by using the name and date of birth of the child and her
parents, linking them to the Danish Central Person Registry (CPR).

We transcribe the collection of nurse records by using timmsn, a Python
library for image-to-text translation [72]. The library is based on the
PyTorch Image Models library by [101], an image recognition Python library.
The full transcription code is available upon request and will be made
available open-source at https://github.com/TorbenSDJohansen/cihvr-
transcription. For the interested reader we refer to Appendix B for additional
details. We transcribe most of the contents of the nurse records with between
95%-99% accuracy, with slightly lower transcription accuracy of around 93% for
nurse names (see Appendix Table B.3 for details).

#### Data Linkage and Coverage

We link the collection of nurse records to administrative data using the
unique CPR number (similar to the US Social Security Number) of the children
of the records. Figure 2 shows the process from the raw, scanned nurse records
to the link with outcomes from Danish registers. While the full collection of
scanned nurse records consist of 95,323 documents, some of these we identify
as duplicates and others as non-records (e.g., notice of movement), leading to
a total of 92,902 records (of which 92,279 contain date of birth, which we
need to obtain the children’s CPR numbers). Some records we are unable to link
to the Danish CPR, which may be due to poor scan quality or death prior to the
establishment of the CPR in 1968, leaving us with 88,808 records we are able
to link to the CPR. Note, however, that 808 of these children do not result in
a match with our administrative data (which starts in 1977), primarily due to
emigration or death, leaving us with a sample of 88,000 records (children) we
can link to administrative outcome data. For the majority of our analyses, we
shall make use of information on the nurse visiting the child and the district
of the nurse; constraining the sample to only those records (children) with
this information brings the sample size down to 75,318.303030Here, we also
restrain the sample to records on which the name of the nurse occur at least
100 times across the entire collection of nurse records. This is done for two
reasons: First, for confidentially reasons we are not allowed to report
estimates of small group sizes, and once we combine nurse name information
with year and district information, subgroups otherwise become too small.
Second, nurse names that occur rarely are more likely to be artefacts from
transcription, such as an otherwise valid name having been transcribed
slightly incorrectly.

Scanned documents ($n=$ 95,323) Duplicates in scans ($n=892$) Other documents
(e.g., notice of death/movement) ($n=$ 1529) Nurse record ($n=$ 92,902; 92,279
with DOB on record) Record not linked to personal identifier (e.g., poor
quality, death/emigr. prior 1968) ($n=$ 4094) Record linked to personal
identifier: Unique infants in data, alive and in DK in 1968 ($n=$ 88,808)
Record not merged to outome data at Statistics Denmark. Event (1968-1977):
Emigration or lost record (85%), death (12%), other (3%) ($n=$ 808) Sample of
records merged to administrative data at Statistics Denmark (1977-2018) ($n=$
88,000) Lost due to insufficient information: Missing nurse information (30%),
“rare” nurse (65%), no district information (5%) ($n=$ 12,682) Sample with
nurse and district information ($n=$ 75,318)

Figure 2: Flowchart: Linkage and Merge of Scanned Records to Administrative
Data.

Notes: The figure shows the sample size in terms of the scanned nurse records
to the individuals we are able to merge with administrative data. Numbers in
parentheses indicate sample sizes. “Rare” nurse refers to nurses whose names
occur on fewer than 100 records. DOB is shorthand for date of birth. The
sample sizes used for individual analyses might deviate slightly due to less
stringent sample requirements due to (1) nurse name information not being
important or (2) nurse district information not being important.

#### Child-Nurse Matches

Our study relies on identifying the specific nurse responsible for visiting
each child, and further on being able to identify which nurse district each
nurse belonged to, in order for us to be able to compare children within the
same nurse district with each other. To do this, we use our transcriptions of
nurse name for each journal, and merge this with archive material on which
district each nurse belonged to. We have been able to find information listing
for each nurse the district they served in for the years 1957, 1963, 1965 (two
separate accounts), and 1968, and it is this information we use to associate
to each child the nurse district to which they belonged. This is a potential
limitation, as nurses may change district over time, and while the data on
nurse districts cover the entire time span we consider, we lack information
for certain years (if, e.g., a certain nurse in 1964 served in a different
district than in 1963 and 1965) and may have incomplete information on all
nurses (if, e.g., a nurse was employed only in 1964, thus not showing up in
any of the years we observe).

We match nurse records to nurse districts by identifying “most likely” matches
between the nurse name transcriptions of the collection of nurse records with
the archive material listing nurses and their districts. As the number of
different nurses is limited (112), often encountered issues in linking based
on names pertaining to non-unique names is limited. However, we note the
following potential issues: First, while our transcription accuracy is high
(see Appendix Table B.3), it is not perfect, and this will result in a number
of children with an incorrect nurse name transcription, leading to missed
matches.313131However, this is very unlikely to lead to a wrong match, as it
would require a name to be transcribed incorrectly as another name. Further,
we observe that incorrect transcriptions are primarily related to poor scan
quality or source material degradation, both of which are unlikely to lead to
any systematic bias. As such, we mainly view this weakness as one decreasing
our precision, not as one introducing potential bias. Second, nurses would not
always write their name fully out. Specifically, we often observe that nurses
would write their initial (of their first name) as well as their last name,
rather than fully writing out their name. For this reason, we iteratively
match nurses, looking first at exact matches where both first and last name of
nurses are fully written, and then gradually relax this requirement over six
steps.323232In the second step, we – for those we did not match in the
previous step – relax the requirements to allow use of initial in place of
full first name. We then (3) match on first name initial and full last name,
(4) match on full first name, (5) match on full last name, and (6) match on
just first name initial. In cases where any of these steps leads to more than
one match, we select the match closest in time, i.e., if a child is born in
1963 and we match the nurse on her record to our list of nurse districts for
both 1963 and 1965, we select the match from the 1963 nurse district data.
Third, as we only observe certain “snapshots” with respect to the nurses’
districts, we potentially assign a wrong district to some children,
particularly for the years furthest away from when we have information on
nurse districts. For this reason, we experiment with samples where we limit
the maximum time span between a child’s birth and one of our snapshots.

In total, we are able to match 43.1-98.4% of the children with a nurse
district, depending on the strictness of our matching approach.333333This
refers to the share of nurse records with a non-rare nurse name transcription,
of which there are 76,579 in total. This number is slightly higher than the
final sample size shown in Figure 2 due to missing district information for a
few of the 76,579 records. We focus on the larger sample that potentially
includes lower quality matches, but also show robustness of our results to
stricter versions of our matching approach. In total, 112 different nurses
appear across the collection of nurse records, and using our most lenient
method of matching information on nurse district allows us to obtain this
information for 111 of the nurses.

###  4.2 Danish Administrative Data

We combine data from Danish registers to obtain information on long-run
outcomes in the form of education and labor market outcomes. We obtain data
from education and labor market registers for the years 1980-2018/2019,
respectively. From education registers, we obtain information on the years of
completed education of our focal individuals as well as their relatives,
including information on highest completed educational level (e.g., mandatory,
university, etc.). From labor market registers, we obtain information on
employment and earnings of our focal individuals and their relatives. For each
individual, we obtain the share of time in employment during each year for
which we have data, as well as their earnings each year.343434We inflation-
adjust earnings to reflect 2015 values and winsorize one percent of each tail,
the latter which we do separately for each age.  Using our employment and
income data, we obtain average share of time in employment and income during
ages 25-50 for each individual.353535If information is missing for one or
multiple ages of an individual during these 25 years, we take the average of
the ages with non-missing employment/income information.

##  5 Empirical Methods

Directly comparing outcomes of children for whom different nurses were
allocated is likely to lead to false conclusions given significant differences
in resources across different areas of Copenhagen (such as a family’s
available resources). To account for such differences, we make use of nurse
districts and information on year of birth, exploiting that children born
within a district-by-year group are likely to be “as good as randomly”
assigned a nurse from that district.363636In Section 6, we empirically verify
this by comparing pre-treatment characteristics of children allocated
different nurses but born within the same district-by-year group. Given that
each nurse was supposed to be responsible for around 160 children, the birth
of a new child in a district is likely to be assigned to the nurse from that
district with the smallest current workload. Given that the Copenhagen nurse
program followed all children during their first year of life, the allocation
of a child to a nurse within a district is likely to be as good as random.

Cast in terms of the potential outcomes framework, we assume the potential
outcomes of a child are independent of the nurse visiting the child, at least
conditionally on the nurse district-by-year.373737Conditioning on the district
might be important if, e.g., the potential outcomes of a child changes if the
child lived in another district where, e.g., the schools were better. Further,
the parents of children in one district might vary systematically from the
parents of children in another district, for instance reflecting socioeconomic
differences. Letting $Y_{id}^{j}$ denote the potential outcome of child $i$ in
district-by-year $d$ under the “treatment” (visits) of nurse $j$, we assume:

$\displaystyle Y_{id}^{j}\perp\\!\\!\\!\\!\perp D_{i}^{j}\,|\,G_{id},$ (1)

where $D_{i}^{j}\in\\{0,1\\}$ is one if child $i$ was visited by nurse $j$ and
$G_{id}$ symbols the nurse district-by-year groups. The realized outcome of
child $i$ is then $Y_{id}=\sum_{j}Y_{id}^{j}D_{i}^{j}$, and our objective is
to draw inference on “treatment effects” of the type
$\tau_{ij_{1}j_{2}}=Y_{id}^{j_{1}}-Y_{id}^{j_{2}}$, where now both $j_{1}$ and
$j_{2}$, $j_{1}\neq j_{2}$, represent nurses. This, then, represents the
effect of assigning nurse $j_{1}$ rather than $j_{2}$ to child $i$, i.e., what
is the change in the outcome of child $i$ by re-assigning nurses in such a way
that child $i$ now receives visits form nurse $j_{1}$ rather than nurse
$j_{2}$.

If we knew $Y_{id}^{j}$, we could directly calculate all
$\tau_{idj_{1}j_{2}}$, but in the absence of this, where only the realized
outcome is observed, we turn our attention first to the more coarse treatment
effects of the type
$\tau_{dj_{1}j_{2}}=\mathbb{E}\left[Y_{d}^{j_{1}}\right]-\mathbb{E}\left[Y_{d}^{j_{2}}\right]$,
i.e., where we no longer subscript with $i$, instead averaging over children
to obtain average treatment effects. Given (conditional) random allocation of
nurses to children, this can be estimated by plugging in sample equivalents of
$\mathbb{E}\left[Y_{d}^{j}\right]$, namely
$\frac{1}{\sum_{i}D_{i}^{j}}\sum_{i}D_{i}^{j}Y_{id}$.

Due to potential differences between district-by-year groups we consider the
simplest case, focusing on some specific district-by-year group (and then
leaving out subscripts $d$ for notational simplicity). Here, we may regress an
outcome $Y_{i}$ of individual $i$ on dummy variables $D_{i}^{j}$, where $j$
enumerates the different nurses and where $D_{i}^{j}=1$ if child $i$ was
assigned nurse $j$:

$\displaystyle Y_{i}=\beta_{j}D_{i}^{j}+\epsilon_{i},$ (2)

where $\beta_{j}$ then denotes the expected outcome of children assigned nurse
$j$; thus, our estimate of $\tau_{j_{1}j_{2}}$ is then:

$\displaystyle\hat{\tau}_{j_{1}j_{2}}=\hat{\beta}_{j_{1}}-\hat{\beta}_{j_{2}}=\frac{1}{\sum_{i}D_{i}^{j_{1}}}\sum_{i}D_{i}^{j_{1}}Y_{i}-\frac{1}{\sum_{i}D_{i}^{j_{2}}}\sum_{i}D_{i}^{j_{2}}Y_{i}$
(3)

The above approach allows us to compare the average outcomes of children by
nurse within any specific district-by-year group. A further challenge arises,
however, if we try to compare treatment effect estimates between district-by-
year groups. The reason is as follows: Any treatment effect is a difference in
average potential outcomes between two groups of children, and thus the size
of any treatment effect depends not only on the visiting nurse, but also on
the counterfactual alternative nurse you use as the base for your comparison.
For that reason, large treatment effects might arise from either or both of
(1) the nurse $j_{1}$ being in the right tail of the skill distribution and/or
(2) the nurse $j_{2}$ being in the left tail of the skill distribution. For
those reasons, directly comparing treatment effects between district-by-year
groups is not possible

When we then turn to heterogeneity of nurse effects depending on child pre-
treatment characteristics, we let $X_{i}\in\mathbb{R}^{l}$ denote the vector
of characteristics for child $i$.383838For example, $X_{i}$ might include low
birth weight status or absence of father. We once again consider the simplest
case of one district-by-year group, and now include $X_{i}$ to account for
nurse-by-child-characteristic differences:

$\displaystyle Y_{i}=f\left(D_{i}^{j},X_{i}\right)+\epsilon_{i},$ (4)

where we may use causal ML to estimate heterogeneous treatment effects, such
as generalized random forests [99, 8].393939We use extensions by [86] to allow
estimation in our setting of multi-arm treatments. The heterogeneity we are
able to capture this way reflects the cross-product of differences between
nurses and children and, if present, allow us to consider welfare effects of
nurse reallocation.

Our identification strategy relies on quasi-random allocation of children to
nurses within nurse district-by-year groups. If this is not so, and nurses are
selectively allocated to children as might be the case if children from
families the least well off are more likely to be allocated a specific nurse,
conditional independence between potential outcomes and treatment no longer
holds. To mitigate such concerns, we perform several tests of differences in
pre-treatment variables between the children of different nurses.

##  6 Results

###  6.1 Descriptive Statistics

We start by documenting the number of nurses and the number of children per
year, district, and nurse. We can estimate the number of nurses in two ways,
based on either statistics from archives or directly from the collection of
nurse records we transcribe. From archive material, we know the number of
nurses for the years from which we have data (1957, 1963, 1965-1969). This
includes their names, which allow us to track them over time, allowing us to
calculate the total number of unique nurses. From the collection of nurse
records, we use our transcriptions of nurse names for each record to obtain
statistics on the number of nurses for each year as well as the total number
of unique nurses during the period 1959-1967. Due to imperfect transcriptions,
however, we err on the side of caution and define a nurse only when the name
of the nurse appears on a sufficient number nurse records, to avoid a small
error in a transcription resulting in a name with one letter off now occurring
as a unique nurse with just one record; we require 100 occurrences of a name
to include it.404040Further, due to confidentiality reasons we are required to
aggregate statistics up to include a certain minimum number of children. Table
2 shows the number of nurses for each year as well as the total number of
nurses, as estimated from either archive material or the collection of nurse
records. From the years for which we have data from both archive material and
the nurse records, we generally see slightly fewer nurses from the archive
material than from the nurse records (with 1965 being an exception). This is
expected, as the first reports a snapshot and the second includes nurses
present just for parts of the year.414141For example, a snapshot of nurses for
May may not include a nurse that stopped working in that year before May or
one that started later than May. In total, however, we identify more nurses
from the archive material than from the nurse records; this is also not
surprising as the archive material stretches over a longer period of time
(1957-1969 vs. 1959-1967). In our main analyses, we continue with the sample
of 112 unique nurses, the name of which we know occurred on at least 100 nurse
records.424242In our analyses exploiting information on district we continue
with 111 nurses, due to incomplete district information.

Table 2: Number of Unique Nurses by Year.

| Archive material | Nurse records
---|---|---
1957 | 58 |
1959 |  | 88
1960 |  | 93
1961 |  | 93
1962 |  | 96
1963 | 74 | 99
1964 |  | 101
1965 | 113 | 96
1966 | 64 | 95
1967 | 62 | 93
1968 | 70 |
1969 | 69 |
Total (unique) | 166 | 112

Notes: The table shows the number of unique nurses, identified through either
archive materials or transcriptions of the collection of nurse records. We do
not have an estimate of both sources for each year, which leads to some empty
fields. The final row shows the total number of unique nurses, i.e., the same
nurse present for multiple years counts only once.

Our identification strategy relies on the assumption of random allocation of
children to nurses within each nurse district. From archive material, we know
that the aim of the Copenhagen nurse visiting program was to have each nurse
be responsible for around 160 children, and we would thus expect each nurse at
any point in time to be responsible for somewhere around 160 children ([34],
various years). To assess the number of children by year, district, and nurse,
Figure 3 shows the number of children in our primary sample by year of birth
(Panel 3a), district (Panel 3b), and nurse (Panel 3c). Note that only nurse
names occurring at least 100 times are included.

(a) Children by Year

(b) Children by District

(c) Children by Nurse

Figure 3: Number of Children by Year, District, and Nurse.

Notes: The figure shows the number of children (i.e., nurse records) in our
primary sample by year of birth (Panel 3a), district (Panel 3b), and nurse
(Panel 3c). Note that only nurse names occurring at least 100 times are
included.

As is evident from Figure 3, the number of children by nurse varies
substantially. While this at first appears problematic for our design, this is
explained by differences in how many years the individual nurses were present:
A nurse present in all of the years 1959-1967 will occur on more journals than
one only present in 1959. To gauge the real number of children present at the
same time per nurse, we therefore calculate the number of children by nurse-
year. We do this by calculating the number of children born in each calendar
year for each nurse, and only include a nurse-year if at least one child born
in each month of the given year was assigned to the specific nurse.434343This
is done to eliminate the issue of a nurse only being present for part of a
year. We expect this to lead to a density with high mass centered at close to
but below 160 (given that our sample includes close to but not all of the
potential children of the nurse program and the program aimed at each nurse
being allocated around 160 children). Indeed, Figure 4, which shows the
density of nurse-years as well as district-years, exhibits this pattern: Panel
4a shows the density of the number of children by nurse-year, which exhibits a
tight center of mass, with the average number of children by nurse-year being
around 140. Turning to Panel 4b, which shows the density of the number of
children by district-year, there is more dispersion, indicating that some
districts were larger than others in terms of number of children in the
district. Appendix Figure C.1 shows the number of children within each
district-by-year combination, showcasing that districts that were larger at
the start of the period (1959) generally continue to be so over all the
available years (1959-1967). Further, as we would expect, the number of nurses
is larger in those districts with more children.

(a) Children by Nurse-Year

(b) Children by District-Year

Figure 4: Number of Children by Nurse-Year and District-Year.

Notes: The figure shows the density of the number of children by nurse-year
(Panel 4a) and district-year (Panel 4b).

Table 3 shows means, standard deviations, and number of observations for pre-
treatment and outcome variables for our primary sample, with the last column
showing p-values from a Kruskal-Wallis H-test for independent samples [80],
comparing the population of nurses against each other with a null-hypothesis
of no difference in the median outcome of children of different
nurses.444444Testing for differences in means (i.e., an ANOVA test) leads to
the same picture, but we prefer the Kruskal-Wallis test due to its milder
assumptions. If children were randomly assigned nurses, we would expect the
p-values of the pre-treatment variables (Panel A) to be large, while the
p-values of the outcome variables (Panel B) could still be small if nurses
differed with respect to their treatment effect. However, as is clear from the
table there are statistically significant differences between nurses in all
measures, with the largest p-value being for sex (0.069). This is not
surprising, given that nurses served in different districts (and time periods)
with different populations of children, due to, e.g., different levels of
socioeconomic status of the parents of our focal individuals between nurse
districts.

Table 3: Descriptive Statistics.

| Mean | Standard deviation | No. of obs. | P-value
---|---|---|---|---
Panel A: Background Characteristics, Nurse Records & Administrative Data
Birth weight (g) | 3,326.76 | 527.81 | 76,467 | 0.000
Low BW | 0.05 | 0.22 | 76,467 | 0.000
Birth length (cm) | 51.42 | 2.40 | 76,257 | 0.000
Born prior to due date | 0.12 | 0.33 | 75,118 | 0.000
Weeks prior to due date | 3.41 | 1.87 | 8,619 | 0.001
Year of birth | 1,963.12 | 2.53 | 75,899 | 0.000
Born 1-3 | 0.10 | 0.30 | 75,899 | 0.015
Child parity | 1.63 | 0.79 | 75,184 | 0.000
Firstborn | 0.53 | 0.50 | 75,184 | 0.000
Female | 0.49 | 0.50 | 75,360 | 0.069
Mother yrs. of educ. | 11.25 | 3.13 | 72,303 | 0.000
Mother age at birth | 25.17 | 5.38 | 75,184 | 0.000
Father yrs. of educ. | 12.37 | 3.40 | 64,494 | 0.000
Father age at birth | 28.41 | 6.67 | 72,087 | 0.000
Father missing | 0.06 | 0.23 | 76,579 | 0.000
High SES, 1 mo. | 0.12 | 0.32 | 49,942 | 0.000
Panel B: Outcome Measures, Nurse Records & Administrative Data
Breastfed, 1 mo. | 0.58 | 0.49 | 70,452 | 0.0
Breastfed, 6 mo. | 0.03 | 0.17 | 63,670 | 0.0
Duration of breastfeeding (mo.) | 2.50 | 2.86 | 64,853 | 0.0
Avg. inc. 25-50 (DKK) | 269,452.55 | 162,909.39 | 74,922 | 0.0
Share empl. 25-50 | 0.79 | 0.28 | 74,168 | 0.0
Yrs. of educ. | 13.74 | 2.54 | 74,167 | 0.0
Above mand. edu. | 0.74 | 0.44 | 74,167 | 0.0

Notes: The table shows means, standard deviations, and number of observations
for pre-treatment (Panel A) and outcome (Panel B) variables. Additionally, the
final column shows the p-value from a Kruskal-Wallis H-test for independent
samples, comparing the groups of children of different nurses against each
other. Note that Weeks prior to due date is reported only for those children
born at least a week prior to their due date, which is what explains the low
number of observations and the large value of the mean of this variable.

While Table 3 document statistically significant differences between the
groups of children of different nurses, it does little to report on the
magnitudes of the differences. Table 4 shows statistics for the variables of
Table 3, but where, for each variable, results are grouped by “nurse
rank”:454545This is done separately for each variable, meaning that the order
of nurses vary to some degree between different rows of the table. However,
the rank-order correlation between variables is high, and thus those nurses
for whom the average outcome of one variable of their allocated children is
high also tend to score highly on other variables. Nurses for whom the average
outcome of the given variable of the children they visit is below the first
quantile forms the first group, the second group consists of those between the
first and second quantile, the third group of those between the second and
third quantile, and the final group of those above the third quantile. If
nurses were randomly allocated across all districts, we would expect to see
relatively little difference between the different groups for the variables in
Panel A, and large differences in Panel B only if significant heterogeneity in
nurse treatment effects is present.464646Some variation is still expected due
to finite sample sizes. However, as is clear even for the pre-treatment
variables, differences are also economically large between nurses, implying
differences due to, e.g., variation in socioeconomic status between nurse
districts (e.g., the difference between the lowest ranked quarter of nurses
vs. the highest ranked quarter of nurses in mother years of education is over
one year).

Table 4: Descriptive Statistics by Nurse Group (Rank).

| Mean (std. dev) by quartile | No. of obs.
---|---|---
| 0-25% | 25-50% | 50-75% | 75-100% |
Panel A: Background Characteristics, Nurse Records & Administrative Data
Birth weight (g) | 3,284.49 (536.91) | 3,313.56 (528.39) | 3,334.62 (531.45) | 3,357.27 (515.09) | 76,467
Low BW | 0.04 (0.19) | 0.05 (0.21) | 0.05 (0.23) | 0.07 (0.25) | 76,467
Birth length (cm) | 51.23 (2.47) | 51.37 (2.42) | 51.46 (2.41) | 51.59 (2.32) | 76,257
Born prior to due date | 0.09 (0.29) | 0.12 (0.32) | 0.13 (0.34) | 0.15 (0.36) | 75,118
Weeks prior to due date | 3.08 (1.62) | 3.32 (1.82) | 3.48 (1.88) | 3.74 (2.06) | 8,619
Year of birth | 1,961.01 (1.75) | 1,962.88 (2.48) | 1,963.36 (2.46) | 1,964.81 (1.84) | 75,899
Born 1-3 | 0.08 (0.27) | 0.09 (0.29) | 0.10 (0.30) | 0.12 (0.32) | 75,899
Child parity | 1.54 (0.72) | 1.60 (0.76) | 1.64 (0.80) | 1.71 (0.86) | 75,184
Firstborn | 0.49 (0.50) | 0.52 (0.50) | 0.54 (0.50) | 0.58 (0.49) | 75,184
Female | 0.46 (0.50) | 0.48 (0.50) | 0.50 (0.50) | 0.52 (0.50) | 75,360
Mother yrs. of educ. | 10.55 (2.98) | 10.99 (3.05) | 11.36 (3.12) | 11.79 (3.20) | 72,303
Mother age at birth | 23.97 (4.76) | 24.78 (5.21) | 25.32 (5.42) | 26.14 (5.67) | 75,184
Father yrs. of educ. | 11.61 (3.34) | 12.06 (3.37) | 12.50 (3.37) | 13.01 (3.37) | 64,494
Father age at birth | 27.23 (6.31) | 28.00 (6.48) | 28.60 (6.75) | 29.38 (6.86) | 72,087
Father missing | 0.04 (0.20) | 0.05 (0.23) | 0.07 (0.25) | 0.08 (0.27) | 76,579
High SES, 1 mo. | 0.02 (0.13) | 0.05 (0.22) | 0.10 (0.31) | 0.31 (0.46) | 49,942
Panel B: Outcome Measures, Nurse Records & Administrative Data
Breastfed, 1 mo. | 0.49 (0.50) | 0.56 (0.50) | 0.59 (0.49) | 0.64 (0.48) | 70,452
Breastfed, 6 mo. | 0.01 (0.09) | 0.02 (0.14) | 0.03 (0.17) | 0.06 (0.23) | 63,670
Duration of breastfeeding (mo.) | 1.81 (2.42) | 2.40 (2.75) | 2.61 (2.94) | 3.01 (3.09) | 64,853
Avg. inc. 25-50 (DKK) | 248,926.10 (156,939.84) | 260,964.34 (162,325.75) | 271,131.54 (161,560.47) | 285,750.18 (166,404.97) | 74,922
Share empl. 25-50 | 0.76 (0.30) | 0.78 (0.29) | 0.80 (0.27) | 0.82 (0.26) | 74,168
Yrs. of educ. | 13.34 (2.49) | 13.57 (2.51) | 13.79 (2.55) | 14.08 (2.55) | 74,167
Above mand. edu. | 0.69 (0.46) | 0.72 (0.45) | 0.75 (0.44) | 0.79 (0.41) | 74,167

Notes: The table shows means (standard deviations) for pre-treatment variables
(Panel A) and outcome variables (Panel B) by different groups of nurses, as
defined by their rank compared to other nurses. Nurses for whom the average
outcome of the given variable of the children they visit is below the first
quantile forms the leftmost group (0-25%), while the next group consists of
those between the first and second quantile, the third group of those between
the second and third quantile, and the final group of those above the third
quantile.

To get a more detailed look into the distribution of variables by nurse,
Figure 5 shows mean values (and associated 95% confidence intervals) of
selects pre-treatment (i.e., determined before visit by nurse) variables by
nurse, ranked such that nurses are sorted in ascending order. As expected
following the results in Panel A of Table 4, the figure shows significant
differences in averages of pre-treatment variables by nurse, indicating that
the population of children allocated different nurses vary substantially; as
these variables are determined before the visits take place, the differences
cannot be explained by differences in nurse treatment effects, but must
instead occur due to non-random allocation.

(a) Low BW ($<$ 2500 g)

(b) Mother years of education

Figure 5: Pre-Treatment Variables by Nurse.

Notes: The figure shows means and 95% confidence intervals for select pre-
treatment (i.e., determined before visit) variables by nurse, where nurses are
sorted in ascending order in terms of the mean of the variable for the
children allocated to the specific nurse. Panel 5a shows the results for an
indicator of low birth weight (defined as a birth weight below 2500 g) and
Panel 5b for the years of education of the mother of the child.

Another way of assessing the degree of sorting that happens between nurses and
children is to ask what the rank-order correlations between pre-treatment and
outcome variables are. In a setting of no sorting, this would be
(asymptotically) zero: While children that score “poorly” on pre-treatment
characteristics (e.g., someone born low birth weight) are expected to score
poorer on outcome variables (e.g., income), we would expect zero rank-order
correlation between the average value of a pre-treatment and an outcome
variable between nurses. We therefore calculate these averages for each nurse
for select variables and then use a Spearman rank-order correlation (a non-
parametric measure of monotonicity) to compare nurses [49].474747With 112
nurses, the asymptotic approximation of the p-value may yet be inaccurate, and
the exact p-value is computationally impossible to derive. For these reasons,
we use a permutation test that randomly draws 100,000 permutations,
calculating the rank-order correlation coefficient of each and then compares
it to the rank-order correlation coefficient of the non-permuted sample,
letting the p-value be the share of permutations that results in a more
extreme value of the rank-order correlation coefficient.  Appendix Figure C.2
shows the correlation coefficients and p-values for pairs of select pre-
treatment and outcome variable means by nurses, verifying that substantial
rank-order correlation is present, also when comparing pre-treatment and
outcome variable pairs.

Taken at face value, the above results could be interpreted as detrimental to
our identification strategy. However, the differences we observe between
nurses turn out to be explained largely by differences between nurse districts
(and to a smaller extent differences between cohorts). Figure 6 shows the
equivalent of Figure 5 but now by nurse district rather than nurse. Notably,
the variability of pre-treatment mean outcomes between districts is nearly as
large as the variability of mean outcomes between nurses.484848Note that the
minimum and maximum mean outcomes of a district are bounded by the most
extreme values of mean outcomes of any nurse. The same pattern emerges when we
consider the rank-order correlation in means of variables between districts
(similarly to what we did above for nurses): Appendix Figure C.3 shows the
correlation coefficients and p-values for pairs of select pre-treatment and
outcome variable means by nurse districts, verifying that substantial rank-
order correlation is present, also when comparing pre-treatment and outcome
variable pairs.494949With 16 nurse districts, the asymptotic approximation of
the p-value will be inaccurate, and the exact p-value is computationally
impossible to derive. For these reasons, we use a permutation test that
randomly draws 100,000 permutations, calculating the rank-order correlation
coefficient of each and then compares it to the rank-order correlation
coefficient of the non-permuted sample, letting the p-value be the share of
permutations that results in a more extreme value of the rank-order
correlation coefficient.

(a) Low BW ($<$ 2500 g)

(b) Mother years of education

Figure 6: Pre-Treatment Variables by Nurse District.

Notes: The figure shows means and 95% confidence intervals for select pre-
treatment (i.e., determined before visit) variables by nurse district, where
districts are sorted in ascending order in terms of the mean of the variable
for the children allocated a nurse in the given district. Panel 6a shows the
results for an indicator of low birth weight (defined as a birth weight below
2500 g) and Panel 6b for the years of education of the mother of the child.

Differences in outcomes between districts persist throughout life: Figure 7
shows income and share of time in employment for our focal individuals during
ages 25-50 by nurse district. While there is some variability, those districts
“doing well” in the early years of the focal individuals’ lives tend to do so
throughout their life-cycle.505050We end at age 50 as that is about the
highest age for which we observe the outcomes for all our focal individuals.

(a) Income (DKK)

(b) Employed

Figure 7: Life-Cycle Outcomes by Nurse District: Ages 25-50.

Notes: The figure shows the average income (Panel 7a) and share of time in
employment (Panel 7b) for our focal individuals during ages 25-50. Each line
represents a separate nurse district, and its value is the average value of
the respective variable at the given age.

We claim these differences between districts (and to a smaller extent cohorts)
largely drive the apparent non-random allocation of children to nurses, and
that properly handling this leads to close-to random allocation within
district-by-year groups (see Appendix Figure 4 for district-by-year group
sample sizes). To show this, we once again turn to the rank-order correlation
coefficient tests we performed above for nurses, but now do so within each
district-by-year group of our sample. This leads to 137 (instead of 144, due
to a few district-by-year groups containing exactly one nurse) separate
district-by-year groups, and for each we obtain the p-value for the Spearman
rank-order correlation coefficient test.515151The number of nurses within each
district-by-year group vary, and we thus apply a flexible inference approach
that calculates the exact p-value whenever this is possible in fewer than
10,000 permutations and otherwise sample 10,000 permutations at random. Figure
8 shows the empirical cumulative density function (CDF) of the p-values
obtained this way (colored lines). The black, dashed line indicates the
asymptotic CDF given no rank-order correlation; given random allocation of
children to nurses within these district-by-year groups, we expect the pairs
with (at least) one pre-treatment variable to lie close to this line. Indeed,
we also see this pattern, while also observing that the rank-order correlation
between average income during ages 25-50 and years of education is
statistically significant, which implies that while nurses did appear to have
been allocated children at random, the children they visited systematically
differ in how well they fare during their life.

Figure 8: Rank-Order Correlation CDF of Mean Outcomes by Nurses Within Same
District-by-Year.

Notes: The figure shows p-values from Spearman rank-order correlation tests.
For each district-by-year group, we obtain the mean value of each variable for
each nurse, and we then calculate the rank-order correlation between nurses
(i.e., comparing the ranks of nurses within the district-by-year group for one
variable with the ranks of nurses for another variable, again within the
specific district-by-year group). To obtain p-values, we apply a flexible
inference approach that calculates the exact p-value whenever this is possible
in fewer than 10,000 permutations and otherwise sample 10,000 permutations at
random. For each pair of variables, we then plot the empirical CDF of the
obtained p-values. The jump at $0.5$ arise as a consequence of the presence of
district-by-year groups with exactly two nurses.525252Exact p-values are 0.5
by design in such cases, adding mass to the midpoints.

To further investigate whether some selection between nurses could still take
place within the district-by-year groups, we return to our earlier strategy to
non-parametrically compare groups of children allocated different nurses by
means of a Kruskal-Wallis H-test for independent samples [80]. Now, however,
we do so separately for each district-by-year group and then plot the
empirical CDF (as well as the theoretical CDF given no selection). Figure 9
shows the results for select pre-treatment variables, with each colored line
representing a pre-treatment variable and the black, dashed line indicating
the theoretical CDF given no selection. Reassuringly, all empirical CDFs lie
relatively close to the dashed line, indicating limited differences between
groups of children allocated different nurses (within district-by-year
groups); however, differences do not vanish entirely for all variables.

Figure 9: Non-Parametric P-Values for Differences Between Samples of Children
by Nurse within District-by-Year: Pre-Treatment Variables.

Notes: The figure shows empirical CDFs for p-values obtained from a Kruskal-
Wallis H-test for independent samples for select pre-treatment variables.
Within each district-by-year group, we test for differences in medians for
groups of children allocated different nurses.

###  6.2 Estimation Results

Having established what appears to be close-to random allocation of children
to nurses within nurse district-by-year groups, we next turn to estimating the
“treatment effects” of nurses. Since children appear to have been more or less
randomly allocated a nurse from the population of nurses in the district-by-
year group they belong to, we can estimate the average potential outcome of
children assigned a specific nurse by simply calculating the sample average
for that nurse. First, however, we verify that such differences are indeed
present.

Figure 10 shows empirical CDFs for p-values from a Kruskal-Wallis H-test for
independent samples between nurses in the same district-by-year group for
select outcome variables (i.e., done similarly to Figure 9 but now for
outcomes). Panel 10a shows results for childhood outcomes (obtained from the
nurse records within the first year of a child’s life) and Panel 10b for
adulthood outcomes (obtained from registers). The colored lines indicate
outcomes and the dashed, black lines the theoretical CDFs in a setting of no
differences between samples. As is evident from both panels, and particularly
so for the childhood outcomes of Panel 10a, the empirical CDFs lie far above
the black, dashed lines, indicating statistically significant differences
between groups of children allocated different nurses, even when only
comparing against nurses within the same district-by-year. Compared to the
empirical CDFs for pre-treatment variables shown in Figure 9, where the CDFs
were close to the dashed line indicating no differences between groups, there
now emerge differences far more statistically significant.

(a) Childhood outcomes

(b) Adulthood outcomes

Figure 10: Non-Parametric P-Values for Differences Between Samples of Children
by Nurse within District-by-Year: Outcome Variables.

Notes: The figure shows empirical CDFs for p-values obtained from a Kruskal-
Wallis H-test for independent samples for select outcome variables; Panel 10a
for childhood outcomes and Panel 10b for adulthood outcomes. Within each
district-by-year group, we test for differences in medians for groups of
children allocated different nurses.

While the evidence above indicates strong, statistically significant
differences between nurses in terms of their treatment effects, it does little
to gauge the magnitudes of these differences. To illustrate the magnitudes of
the differences, Figure 11 shows box-plots of average outcomes by nurse-year
for each nurse district. Evidently, there is significant heterogeneity both
within and between districts in terms of averages of children allocated
different nurses. Further, as supported by Appendix Figure C.3, districts that
do well on one measure tends to also do well on others. However, while there
are large differences between districts, differences within districts (i.e.,
between nurse-years within the same district) are in some cases larger still.

(a) Years of education

(b) Above mandatory education

(c) Share of time employed 25-50

(d) Average income 25-50

Figure 11: Box Plots of Average Outcomes by Nurse-Year for Each Nurse
District.

Notes: The figure shows box plots of average outcomes by nurse-year for each
district, meaning that each point represents an average of the children
allocated a specific nurse born within a specific year. Panel 11a shows box
plots for average years of education by nurse-year for each of 16 nurse
districts, Panel 11b for the share of individuals attaining higher than
mandatory education, Panel 11c for the share of time in employment during ages
25-50, and Panel 11d for average income during ages 25-50.

While Figure 11 provides an overview of differences within and between nurse
districts, it “aggregates” across cohorts, meaning that each box plot contains
averages for different years, meaning that some of the variation comes from
differences between cohorts rather than nurses. For this reason, Appendix
Figures C.4 and C.5 show equivalents of Panels 11a and 11d of Figure 11,
respectively, but where each panel now refers to a different year of birth of
the children. While the figures are more noisy, significant heterogeneity is
still present both between and within nurse districts, documenting that the
differences of Figure 11 are not solely driven by cohort effects.

A potential concern regarding the differences between nurses documented above
is that they may arise through noise: Since raw averages constitute the points
of the box plots, the variance of these estimates are not accounted for. For
this reason, we plot both the point estimate and its associated 95% confidence
interval for each nurse, split by district and year, in Appendix Figure C.6
(for years of education) and Appendix Figure C.6 (for average earnings during
ages 25-50). While some estimates are relatively imprecise (with wide
confidence intervals), there is nonetheless clear differences between the
outcomes of different nurses, even within the same district-by-year group, and
these differences are economically significant (e.g., cases of more than one
year of education on average between the children of two different nurses
within the same district and year).

While the evidence above supports the hypothesis of differences between nurse
skills leading to differences in outcomes between children allocated different
nurses, its magnitude and interpretation is hampered by the complex setting of
many nurses as well as district-by-year groups. We therefore turn to a simpler
method of assessing what differences can be expected between two groups of
otherwise similar children which happen to be allocated different nurses.
Specifically, we calculate, for each district-by-year group, the average
values of our outcomes by each nurse, and then take all distinct pairs of
nurses and calculate the absolute value of the difference in the the average
values of their children. The average of these absolute differences is then an
estimate of the expected difference between two otherwise similar groups of
children, but which happen to have been allocated different nurses.

Figure 12 shows the empirical distributions of these absolute differences in
the averages of children with different nurses but within the same district-
by-year group, along with the average value of these absolute differences
(black, solid line). As shown, these differences are economically large: For
example, two otherwise similar groups of children that happened to be
allocated different nurses differ, on average, by nearly half a year of
education and around DKK 27,000 in annual earnings (note, however, that large
parts of these differences arise due to considering absolute differences;
nevertheless, as we show later, differences beyond those that might arise due
to noise are present). Further, these differences are not driven by few,
extreme differences, but rather by relatively large differences by a large
share of nurse-pairs.

(a) Breastfed at 1 mo.

(b) Breastfed at 6 mo.

(c) Duration of breastfeeding (mo.)

(d) Years of education

(e) Above mandatory education

(f) Share of time employed 25-50

(g) Average income 25-50

Figure 12: Average Absolute Differences Between Children of Different Nurses
Within Same District-by-Year.

Notes: The figure shows histograms (with associated density plots) of absolute
values of differences in average values of children with different nurses but
within same district-by-year group. The black, solid line in each panel shows
the average of the underlying absolute differences. The different panels refer
to different outcome variables.

While the findings in Figure 12 document large differences in outcomes of
children allocated different nurses, the measure is by design bounded below at
zero, and so the average differences will be larger than zero, even
asymptotically and with no actual differences between nurses. Therefore, we
want to ensure that these differences are not artefacts due to noise but
represent real differences between nurses. However, the complex nature of the
setup does not lend itself well to normal inference, and we therefore turn to
a permutation-based strategy for inference.

Suppose nurses do not differentially affect children, but that potential
outcomes differ by districts and cohorts. Then we could, separately for each
district-by-year group, permute the children, leading us to – in the
counterfactual setting – assign at random $k$ children within the same
district-by-year group to some nurse with $k$ children in the real
setting.535353We need to keep the number of children for each nurse fixed to
not bias our results to show as always significant: Since we measure un-
weighted differences between pairs, removing noise in number of children by
nurse would lead us to over-estimate the statistical significance of our
findings, as this equalization in sample size would reduce statistical noise.
Doing so for each nurse within each district-by-year group, we obtain a
permutation which, if nurses did not differentially affect children, would
follow the same distribution as our actual sample. Repeating this would then
lead to a counterfactual distribution of average absolute differences, and we
can then get an estimate of the exact p-value by calculating the share of
permutations that led to a larger average absolute difference than the one in
the actual data.545454Exact p-values are computationally infeasible, which is
why we only obtain an estimate. The test is designed such that a more extreme
value always corresponds to a greater value, which leads to the right-tail
focus. Specifically, we perform 1000 permutations and obtain for each a
counterfactual estimate of the average absolute difference in the permuted
sample.

Table 5 shows the average absolute differences in outcomes between children of
different nurses and, to take potential differences arising due to noise into
account, the “excess” difference, i.e., the absolute average difference beyond
those obtained on average in the permutation tests. Further, mean values of
outcomes are reported (MDV), and the table also shows p-values obtained from
the permutation tests, i.e., each p-value is the share of times a
counterfactual estimate based on a permutation attained a more extreme value
than the one from the non-permuted sample. As is evident, all the differences
are highly statistically significant, as are they economically significant
(e.g., differences of more than one month in length of education and income
differences of around 1.4%). Appendix Figure C.8 shows, for each variable in
Table 5, histograms of the averages obtained from the permutation tests,
clearly showcasing that the averages obtained in the actual sample are larger
than those which could appear due to random noise.

Table 5: Average Differences in Outcomes by Nurses Within District-by-Year
Groups.

Outcome | Average Difference | Excess Difference | MDV | P-value
---|---|---|---|---
Breastfed, 1 mo. | 0.09 | 0.02 | 0.58 | 0.000
Breastfed, 6 mo. | 0.03 | 0.00 | 0.03 | 0.004
Duration of breastfeeding (mo.) | 0.59 | 0.14 | 2.50 | 0.000
Avg. inc. 25-50 (DKK) | 27,722.42 | 3,767.50 | 269,452.55 | 0.000
Share empl. 25-50 | 0.05 | 0.01 | 0.79 | 0.000
Yrs. of educ. | 0.47 | 0.09 | 13.74 | 0.000
Above mand. edu. | 0.07 | 0.01 | 0.74 | 0.006

Notes: The table shows estimates of average (absolute) differences in outcomes
between two otherwise similar groups of children allocated different nurses
(but within the same district-by-year group). Since the test statistic we use
is not centered around zero, we also report the “excess” difference, which is
the difference between nurses above that which is a result of noise. MDV is
the mean of the dependent variable. The p-values are from permutation-based
tests which randomly match children and nurses within a district-by-year group
and is calculated as the share which results in a more extreme value than the
one observed in the non-permuted data, and we use a Holm–Šidák approach to
account for multiple hypothesis testing.

Taken together, our results showcase large, economically as well as
statistically significant, differences in how well children fare as a
consequence of which nurse they got allocated for their visits during their
first year of life. Further, recall that these estimates are not estimates of
the impact of the nurse visiting program; rather, they are specifically the
differences within the program as a consequence of the visiting nurse. As
such, our findings suggest that an integral part of understanding the impact
of such policies lies in understanding the role of the treatment provider, in
addition to the program itself.

When comparing nurses and nurse “treatment” effects in this setting it is
important, however, to apply some caution: Any treatment effect is a
difference in averages between two nurses within the same nurse district, and
so a large treatment effects may be any one or both of (1) a skilled nurse and
(2) a poor comparison nurse. Further, it is only possible to obtain these
estimates within district-by-year group without imposing stronger assumptions
on the underlying potential outcomes, and thus comparing differences across
district-by-year groups must be done with caution.

###  6.3 Child-Specific Treatment Effects & Allocation Mechanisms

While our results documenting important differences in how well children
allocated different nurses fare are interesting by themselves, and may have
policy implications in terms of added focus on improving the skill of the
worst nurses, some differences are likely impossible to erase, due either to
skills attained only through years of experience or some inherent differences
between nurses which are non-trivial to mitigate, another avenue for potential
gains is in optimally “matching” children and nurses. Our hypothesis posits
that certain children are particularly likely to benefit from a highly skilled
nurse compared to others; for example, perhaps children with poor initial
health or born to parents in the lower end of the socioeconomic distribution
are more likely to benefit from a high rather than low skill nurse compared to
a child born in perfect health to parents from the higher end of the
socioeconomic distribution. If this is the case, there is potentially room for
improved impacts of the nurse visiting program by exploiting such information
to allocate children to nurses in a better way.

For it to be possible to identify potential gains from improving the
allocation mechanism of the nurse visiting program, we require estimates of
treatment effects that take into account such heterogeneity. Further, for any
such allocation mechanism to be feasible, it needs to rely on readily
available information of the child and/or her family.

In terms of relevant information readily available for potential
(re)allocation, the nurse records provide information available immediately
from birth in terms of birth weight and length, sex, and number of weeks born
prior to due date (if relevant), and from administrative data we obtain other
information visible directly at birth in the form of parent characteristics
such as age and education.555555While our use of register data here obviously
was not available at the time of the sample we study, we only use information
from the registers that would have been readily available from the parents and
which, today, is immediately available. Nonetheless, we choose to drop
parents’ years of education, as we observe this only later in the registers
and parents may potentially have obtained additional education between the
birth of their child and the point at which we observe their education.
Specifically, we use birth weight, birth length, born prior to due date (and
number of weeks when applicable), an indicator for born one of the first three
days of a month,565656This is potentially an important factor to consider
given the “Copenhagen trial”, which selected children born during the first
three days of a month to an extended, three year NHV program [12]., parity, an
indicator for sex, mother and father age at birth, and an indicator for nurse
assessment of socioeconomic status of the family (low, average,
high).575757Nurse assessment of the socioeconomic status of the home is not
strictly speaking observed before the first visit, as the nurse records it
during her visit at child age one month. However, it is unlikely to be
affected by the nurse during such a short time span. Our results are robust to
excluding this variable from the list of variables we use to estimate
heterogeneous treatment effects.

With this information, we estimate individual-level treatment effects by means
of a series of multi-arm causal forest [99, 8, 86]:585858These effects are
“individual” in the sense of being specific with respect to the at-birth
information we have available on the child and her family. Two children which
are identical with respect to all our measures will not differ in terms of
their estimated treatment effects. For each district-by-year group, we treat
each nurse as a separate treatment arm and estimate heterogeneous treatment
effects (for each pair of arms, i.e., comparing pairs of nurses) with respect
to the information on the child and her family available to us at her
birth.595959Here, we add a new sample restriction in the form of requiring at
least 100 children per nurse (within our district-by-year groups) for
inclusion, as we otherwise risk imprecise estimates related to very low
estimated propensity scores for some nurses.

Having estimated a multi-arm causal forest for each district-by-year group, we
can use the out-of-bag predictions of the forests to estimate counterfactual
outcome distributions under different treatment allocation mechanisms.
Limiting the counterfactual treatment allocation rules to those feasible
within the nurse program, we can then estimate potential gains in the nurse
visiting program from alternative allocation mechanisms. Further, we can
estimate the total room for gains from an alternative allocation rule by
estimating the gains from the optimal allocation mechanism, something which we
proved, in Section 2, is always possible in strongly polynomial time.

Table 6 shows estimated average values of our outcome variables under the
current as well as under two alternative allocation mechanisms: One uses a
greedy heuristic to identify gains from re-allocation (but which is not
guaranteed to achieve the optimal allocation) and one finds the optimal
allocation. The results indicate economically significant room for
improvements: Our estimates for average earnings during ages 25-50 suggest
that improved allocation of nurses to children could have resulted in
additional yearly income of around (2023) USD 1,815.606060We arrive at this
number by adjusting for Danish inflation between 2015 and 2023 (17%) and using
an exchange rate of 0.14 DKK/USD. Turning to education, we estimate the total
gains in terms of length of education to be around two months on average.

Table 6: Outcomes Under Alternative Allocation Mechanisms.

| Allocation mechanism |
---|---|---
Outcome | Actual | Greedy | Optimal | No. of obs.
Breastfed, 1 mo. | 0.58 | 0.60 | 0.62 | 43,259
Breastfed, 6 mo. | 0.03 | 0.04 | 0.04 | 31,449
Duration of breastfeeding (mo.) | 2.55 | 2.63 | 2.74 | 33,139
Avg. inc. 25-50 (DKK) | 275,018.01 | 280,699.60 | 286,100.90 | 50,108
Share empl. 25-50 | 0.80 | 0.81 | 0.82 | 49,186
Yrs. of educ. | 13.83 | 13.92 | 14.00 | 48,916
Above mand. edu. | 0.76 | 0.77 | 0.79 | 48,916

Notes: The table shows estimates of average values of outcomes under
alternative allocation mechanisms, estimated separately for each outcome. The
leftmost rule (“Actual”) reports the actual averages as they are under no new
allocation rule. The next rule (“Greedy”) shows the results of employing a
heuristic, greedy re-allocation mechanism. The final rule (“Optimal”) shows
the results obtained when optimally allocating nurses to children.

How much of the gains from improved allocation is attainable through a simpler
re-allocation algorithm? To answer this question, Table 6 reports results from
a re-allocation mechanism that attempts to find re-allocations using a greedy
heuristic (the column “Greedy”). Specifically, it keeps track of the number of
children allocated each nurse and then goes through each child in a district-
by-year group and allocates the nurse to that child that (1) is not yet at
capacity and (2) results in the highest potential outcome for that child (thus
obtaining an $\mathcal{O}(n_{2})$ re-allocation mechanism). However, as is
clear from our estimates, using this heuristic algorithm leaves significant
room for improvements. This highlights the importance of an exact algorithm
for complex tasks like optimal treatment allocation, emphasizing the value of
deriving a strongly polynomial algorithm for this task.

While Table 6 documents significant room for average improvements through an
optimized nurse allocation mechanism, it potentially hides important ways in
which these average improvements are obtained: If those children currently the
worst off are negatively impacted (e.g., through complementarity of initial
conditions and nurse skill leading to matching of the best nurses to the best
off children), welfare may not be improved under the re-allocation (in terms
of a social planner with preferences for equality). Conversely, if those
children the worst off are (particularly) positively impacted (e.g., through
substitutability of initial conditions and nurse skill leading to matching of
the best nurses to the worst off children), welfare may be more positively
impacted under re-allocations compared to what the average improvement
suggests (in terms of a social planner with preferences for equality).

To study the impact of nurse re-allocation on the distribution (rather than
just its expectation) of outcomes, Figure 13 shows the distribution of our
non-binary outcomes under the current as well as under the optimal allocation
mechanisms.616161Binary outcomes are left out as Table 6 (i.e., their
expectations) fully captures the effects on these. Across the outcomes, we
observe a shift to the right across the entire distribution when moving from
the actual to the optimal allocation, suggesting neither strong
complementarity nor substitutability.

(a) Duration of breastfeeding (mo.)

(b) Years of education

(c) Share of time employed 25-50

(d) Average income 25-50

Figure 13: Realized and Counterfactual Distributions of Outcomes by Nurse
Allocation Mechanism.

Notes: The figure shows the actual and estimated counterfactual distributions
of outcome variables by nurse allocation mechanism. Each panel shows the
current distribution of an outcome variable (in blue) and the estimated
counterfactual distribution under optimal allocation of nurses (in red).

###  6.4 Robustness Checks

The biggest concern to our empirical design is selection in the allocation
mechanism: If children with relatively good potential outcomes are selectively
allocated to one nurse, and children with relatively poor potential outcomes
to another, then our estimates of the differences in treatment effects between
nurses will be biased.

To mitigate such potential concerns, Table 7 shows average differences in
children pre-treatment variables by nurse (with associated p-values from
permutation tests), i.e., similarly to Table 5 but now for pre-treatment
rather than outcome variables. A necessary condition for our assumption of no
selective allocation within district-by-year groups is that differences in
pre-treatment variables should not differ between groups of children allocated
different nurses. Indeed, with the exception of “born prior to due date”, the
estimated differences are at most marginally significant.626262The “excess”
difference in the share of children born prior to due date between nurses is
around one percent. However, the number of weeks born prior to due date does
not systematically differ between children. We interpret this as differences
between nurses in terms of when they would note a child as being born prior to
due date, with some nurses being stricter than others. While these results do
not rule out potential selection, they are nevertheless reassuring for our
design. Further, Appendix Figure C.9 shows the full distribution of
counterfactual differences from our permutation tests (similarly to Appendix
Figure C.8, but for pre-treatment rather than outcome variables).

Table 7: Average Differences in Pre-Treatment Variables by Nurses Within
District-by-Year Groups.

Outcome | Average Difference | Excess Difference | MDV | P-value
---|---|---|---|---
Low BW | 0.03 | 0.00 | 0.05 | 0.119
Born prior to due date | 0.06 | 0.01 | 0.12 | 0.000
Weeks prior to due date | 0.56 | 0.03 | 3.41 | 0.290
Born 1-3 | 0.05 | 0.00 | 0.10 | 0.252
Female | 0.07 | -0.00 | 0.49 | 0.924
Father missing | 0.03 | -0.00 | 0.06 | 0.924

Notes: The table shows estimates of average (absolute) differences in pre-
treatment variables between two otherwise similar groups of children allocated
different nurses (but within the same district-by-year group). Since the test
statistic we use is not centered around zero, we also report the “excess”
difference, which is the difference between nurses above that which is a
result of noise. MDV is the mean of the dependent variable. The p-values are
from permutation-based tests which randomly match children and nurses within a
district-by-year group and is calculated as the share which results in a more
extreme value than the one observed in the non-permuted data, and we use a
Holm–Šidák approach to account for multiple hypothesis testing.

Could our relatively lenient strategy for matching nurse records and nurse
district information introduce some potential bias? To answer this question,
we re-estimate the average differences in outcomes of children between nurses,
similarly to Table 5, but now for a subsample where records are only included
if we can match it to nurse district information using nurse first name
initial and full last name. Table 8 shows our findings, indicating that our
results are robust to this additional sample restriction. Magnitudes remain
relatively stable and our estimated differences are still highly statistically
significant.

Table 8: Average Differences in Outcomes by Nurses Within District-by-Year
Groups: Stricter Matching Criteria.

Outcome | Average Difference | Excess Difference | MDV | P-value
---|---|---|---|---
Breastfed, 1 mo. | 0.09 | 0.02 | 0.58 | 0.000
Breastfed, 6 mo. | 0.03 | 0.00 | 0.03 | 0.003
Duration of breastfeeding (mo.) | 0.59 | 0.15 | 2.50 | 0.000
Avg. inc. 25-50 (DKK) | 27,965.44 | 4,221.04 | 269,780.38 | 0.000
Share empl. 25-50 | 0.05 | 0.01 | 0.79 | 0.004
Yrs. of educ. | 0.46 | 0.09 | 13.74 | 0.000
Above mand. edu. | 0.07 | 0.01 | 0.74 | 0.009

Notes: The table shows estimates of average (absolute) differences in outcomes
between two otherwise similar groups of children allocated different nurses
(but within the same district-by-year group), and where we restrict the sample
to those with a nurse match based on nurse first name initial and full last
name. Since the test statistic we use is not centered around zero, we also
report the “excess” difference, which is the difference between nurses above
that which is a result of noise. MDV is the mean of the dependent variable.
The p-values are from permutation-based tests which randomly match children
and nurses within a district-by-year group and is calculated as the share
which results in a more extreme value than the one observed in the non-
permuted data, and we use a Holm–Šidák approach to account for multiple
hypothesis testing.

Another potential concern is misclassification of children to districts as a
result of nurses changing districts over time and us only observing nurse
district for a subset of our sample years (1963 and 1965). To mitigate such
concerns, we re-estimate the average differences in outcomes of children
between nurses, but now for a subsample where records are only included if the
child is born in one of the years for which we have data on nurse district.
Table 9 shows our findings, indicating that our results are robust to this
additional sample restriction. The magnitudes of our estimates for this
restricted sample are close to the results of Table 5, though less precisely
estimated.

Table 9: Average Differences in Outcomes by Nurses Within District-by-Year
Groups: Stricter Year of Birth Criteria.

Outcome | Average Difference | Excess Difference | MDV | P-value
---|---|---|---|---
Breastfed, 1 mo. | 0.08 | 0.01 | 0.56 | 0.141
Breastfed, 6 mo. | 0.03 | 0.00 | 0.03 | 0.087
Duration of breastfeeding (mo.) | 0.52 | 0.09 | 2.39 | 0.012
Avg. inc. 25-50 (DKK) | 28,080.40 | 4,449.58 | 274,341.07 | 0.036
Share empl. 25-50 | 0.05 | 0.01 | 0.80 | 0.015
Yrs. of educ. | 0.45 | 0.09 | 13.80 | 0.007
Above mand. edu. | 0.07 | 0.01 | 0.76 | 0.141

Notes: The table shows estimates of average (absolute) differences in outcomes
between two otherwise similar groups of children allocated different nurses
(but within the same district-by-year group), and where we restrict the sample
to those born in the years 1963 or 1965 (the years exactly coinciding with our
data on nurse districts). Since the test statistic we use is not centered
around zero, we also report the “excess” difference, which is the difference
between nurses above that which is a result of noise. MDV is the mean of the
dependent variable. The p-values are from permutation-based tests which
randomly match children and nurses within a district-by-year group and is
calculated as the share which results in a more extreme value than the one
observed in the non-permuted data, and we use a Holm–Šidák approach to account
for multiple hypothesis testing.

What role might spillover effects between siblings introduce, and could nurses
be selectively allocated children from families of which they already were
assigned previous children? Table 10 shows our estimates of average
differences in outcomes of children between nurses, but now for a sample of
only firstborn children. Here, some of our results are slightly attenuated
(when compared to Table 5), but the same overarching pattern remains, again
statistically significantly estimated.

Table 10: Average Differences in Outcomes by Nurses Within District-by-Year
Groups: Firstborn Children.

Outcome | Average Difference | Excess Difference | MDV | P-value
---|---|---|---|---
Breastfed, 1 mo. | 0.10 | 0.01 | 0.61 | 0.020
Breastfed, 6 mo. | 0.03 | 0.00 | 0.03 | 0.059
Duration of breastfeeding (mo.) | 0.65 | 0.13 | 2.59 | 0.000
Avg. inc. 25-50 (DKK) | 31,249.23 | 1,927.78 | 278,822.14 | 0.090
Share empl. 25-50 | 0.05 | 0.00 | 0.80 | 0.114
Yrs. of educ. | 0.51 | 0.06 | 13.98 | 0.012
Above mand. edu. | 0.08 | 0.01 | 0.77 | 0.039

Notes: The table shows estimates of average (absolute) differences in outcomes
between two otherwise similar groups of children allocated different nurses
(but within the same district-by-year group), and where we restrict the sample
to firstborn children. Since the test statistic we use is not centered around
zero, we also report the “excess” difference, which is the difference between
nurses above that which is a result of noise. MDV is the mean of the dependent
variable. The p-values are from permutation-based tests which randomly match
children and nurses within a district-by-year group and is calculated as the
share which results in a more extreme value than the one observed in the non-
permuted data, and we use a Holm–Šidák approach to account for multiple
hypothesis testing.

Our above placebo tests and results for alternative samples, combined with our
earlier tests for rank-order correlation between pre-treatment and outcome
variables by nurse within district-by-year groups (see Figure 8) and our non-
parametric tests for differences in pre-treatment variables by nurse within
district-by-year groups (see Figure 9), support our identification strategy.
As far as pre-treatment variables are concerned, there does not appear to have
been significant selection, as long as we only compare nurses within the same
district-by-year group.

###  6.5 Discussion

How do our estimated treatment effects and effects of re-allocation compare to
other early-life interventions? In particular, how much can be gained by
optimizing an existing program – as is the case of the nurse re-allocation –
vs. adding or changing a program with associated increases in required
resources?

The most similar early-life interventions to our setting are the introduction
of NHV programs and center care in Scandinavia [102, 67, 26, 31], as well as
the study by [12] which examines the impacts of extending the Danish NHV
program from one to three years. What sets our setting apart from the studies
above is that we measure the impact of an, in principal, “free” intervention,
which instead of adding resources considers the impact of improved allocation
of existing resources.

Compared to the study on the introduction of NHV in Denmark (1937) by [67],
which finds health effects but none for education and labor market outcomes,
we document positive impacts on education and labor market outcomes. In
Sweden, [26] find that the introduction of a health intervention (pioneered in
1931-1933) that provided information to mothers and infant monitoring through
home visits and clinics led to substantial health benefits and increased
likelihood for secondary schooling enrolment for females by around 3-4%-points
(15%).636363They find no effects on likelihood of secondary schooling
enrolment for males. They interpret this as being due to relatively fixed
supply of schooling during that time. Our estimates suggest that optimal re-
allocation could have improved the probability of completing at least
secondary education by around 3%-points. In Norway, [31] study increased
access to mother and child health care centers during a child’s first year of
life (introduced during the 1930s), finding that access to these centers
improved length of schooling by around 1.8 months and earnings by around 2%,
as well as improved health. Our estimates suggest that optimal re-allocation
could have improved the length of education by around two months and income by
around 4%.

Compared to the above studies on the introduction of early-life policies in
Scandinavia, our results show that, in terms of education and labor market
outcomes, optimally allocating providers (nurses) to recipients (children) may
have effects of similar magnitude. In the US, [68] studies the impact of
county-level health departments (instituted from 1908-1933) on long-run
outcomes, showing that affected men’s later-life earnings were improved by
2-5%, again similar in magnitude to our results. However, our study is set at
a later point in time and focuses not on the introduction but rather the
provision of early-life investments. The closest study to ours in terms of
timing and target group is the study by [12] on the impact of extended NHV
(three vs. one year) for the same group of children comprising our study.
Their findings suggest positive and persistent health effects of enrolment
into the extended NHV program, with some effects on labor market participation
of women (around 1.4%-points for share of time in employment during ages
30-50) but none for education or income. In comparison, our results suggest
that optimal re-allocation could have improved share of time in employment
during ages 25-50 by around 2%-points.

How come our estimates are of similar magnitudes to impacts of introduction of
similar services in Scandinavia and the US? A likely answer lies in findings
across these studies of significant effect heterogeneity, with disadvantaged
children disproportionately positively impacted. Unlike the studies above,
which focus on universal programs, our counterfactual policy focuses precisely
on those children most likely to be positively impacted. We view this as yet
another motivation for studying the role played by treatment providers when
evaluating and designing policies.

##  7 Conclusions

We tackle the issue of solving optimal treatment allocation problems of the
type where each recipient may be differentially affected by each treatment,
and where there are constraints on treatment capacities. We prove that the
problem is solvable in strongly polynomial time and present an algorithm based
on flows in networks for problems of this type. We also extend our algorithm
to cases where only Pareto-improving re-allocations of treatments to
recipients are allowed by modifying the underlying network to ensure that only
re-allocations that make no individual worse off are selected.

To showcase our method, we study NHV in the 1960s Copenhagen. Earlier work in
Denmark, as well as other countries, has documented positive impacts of the
introduction of NHV and center care [102, 67, 26, 31, 68] and extended NHV
[12], but we go beyond these studies by estimating differences in treatment
effects between individual nurses. We do so by transcribing and linking data
from historical nurse records to Danish administrative data, identifying the
nurse allocated each child and following the child throughout her life using
Danish register data.646464This transcription work has been done concurrently
and in collaboration with the work of [28, 12].

We show that outcomes of children vary significantly by the visiting nurse,
even when comparing children in the same nurse district and born the same
year. We show that these differences are not artefacts due to selection (once
operating within district-by-year groups) by comparing pre-treatment variables
between children allocated different nurses. Further, using causal machine
learning, we show that children are heterogeneously affected by nurses. This,
in turn, allows us to obtain estimates of potential outcomes under different
allocation mechanisms, and we document that a re-allocation of the nurses in
the Copenhagen NHV program could have resulted in significant efficiency
improvements. Our estimates suggest that optimal allocation of nurses to
children could have improved average yearly earnings by USD 1,815 (4%) and
length of education by around two months.

We contribute with new knowledge within optimal policy and the literature on
the role of early-life conditions and investments for long-run outcomes.
Within optimal policy, we introduce a strongly polynomial algorithm for
optimal treatment allocation problems under constraints. Within the literature
on early-life investments, we add novel evidence on the role of treatment
providers for the effects of such policies. Further, we show that optimal
allocation of such investments to recipients may play a crucial role in fully
exploiting potential benefits of early-life investments.

While our approach for solving optimal treatment allocation problems is
applicable to settings with various constraints, we assume that potential
outcomes can be sufficiently precisely estimated. Optimal policy learning is a
rapidly evolving field with a number of challenges related to identification.
Directly incorporating policy learning with our approach for solving
allocation problems could prove a fruitful avenue for new research.

For our empirical application, two challenges remain for proper integration of
our optimal allocation design. First, our results for long-run outcomes are
not observable before a significant time-gap, and thus these results are not
directly applicable in practice for estimating potential outcomes. However,
given the strong rank-order correlation between short- and long-run outcomes,
using estimates for short-run outcomes are likely sufficient to obtain re-
allocation rules to improve also long-run outcomes. Second, if all nurses are
re-allocated based on our algorithm, it would no longer be possible to obtain
causal estimates of potential outcomes if the underlying distribution changes
(e.g., as a result of the population of children changing or the population of
nurses changing) since the algorithm by design exploits selection.
Implementing an approach in practice would thus require only partial
selection, leaving some children to be randomly allocated to update estimates
of potential outcomes as its underlying distribution changes. This leaves a
complex “exploration vs. exploiting” problem [95], where the optimal share of
children to randomly allocate to nurses (in order to update estimates of
potential outcomes, i.e., explore) must be decided in a way to optimize
average outcomes over time (i.e., exploit our knowledge to improve allocation
and, in turn, outcomes).

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