covars-interpr-causal.Rnw

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\begin{document}

% \bioctytle
\title{Choosing covariates, interpreting coefficients, and causal inference}

\author{Ramon Diaz-Uriarte\\
  Dept. Biochemistry, Universidad Aut\'onoma de Madrid \\
  Instituto de Investigaciones Biom\'edicas Sols-Morreale, IIBM (UAM-CSIC)\\
  Madrid, Spain{\footnote{r.diaz@uam.es, rdiaz02@gmail.com}} \\
  %% {\footnote{rdiaz02@gmail.com}} \\
  {\small \Burl{https://ligarto.org/rdiaz}} \\
}


\date{\gitAuthorDate\ {\footnotesize (Rev: \gitAbbrevHash)}}



\maketitle

\tableofcontents

\clearpage


%% ZZ: FIXME
%% add numerical examples of everything, including categorical data ones
%% of Simpson's and Berkson's paradoxes

%% And probably teach this before the categorical data analysis part


\section*{License and copyright}\label{license}
This work is Copyright, \copyright, 2025, Ramon Diaz-Uriarte, and is
licensed under a \textbf{Creative Commons } Attribution-ShareAlike 4.0
International License:
\Burl{http://creativecommons.org/licenses/by-sa/4.0/}.

\centerline \ccbysa



All the original files for the document are available (again, under a Creative
Commons license) from \Burl{https://github.com/rdiaz02/BM-1}. (Note that in the
github repo you will not see the PDF, or R files, nor many of the data files,
since those are derived from the Rnw file). This file is called \texttt{covars-interpr-causal.Rnw}.

\vspace*{10pt}

Please, \textbf{respect the copyright and license}. This material is
  provided freely. If you use it, I only ask that you use it according to the
  (very permissive) terms of the license: acknowledging the author and
  redistributing copies and derivatives under the same license. If you have any
  doubts, ask me.

\clearpage

%% \part{The main stuff}

\section{Introduction}

\subsection{What is this about}
\label{sec:what-this-about}

The aim of these notes is to try to clarify  questions about ``what
variables should we add to our models when our aim is interpretation''\footnote{The paper by \cite{keele2020} has a very similar objective: ``(...) we ask when we can justify interpreting two or more coefficients in a regression model as causal parameters. We demonstrate that analysts must appeal to causal identification assumptions to give estimates causal interpretations.''  After going through these notes, reading that paper should be easy.}.

As discussed in class, if our purpose when fitting statistical models is only
prediction, reversal of regression coefficients when a covariate is in the model
with or without other covariates, and other similar counterintuitive phenomena,
are not a problem. The problem can arise if we want to interpret what the
coefficients mean.

The interpretation we often want to give is a causal one. For example, in a model
where the dependent or outcome variable is cardiovascular health and one of the
predictor variables is red wine consumption we are, arguably, trying to
understand if consuming red wine affects (i.e., has an effect on) cardiovascular
health. We might want to do this so that we can make public health
recommendations or take personal action (should I start drinking a little bit of
wine?).  Intuitively, if a variable, X, has a causal effect on a variable, Y,
manipulating X will change the value of Y\footnote{The philosopher James Woodward, in \citet{woodward_making_2003}, defends a manipulationist or interventionist account of causality; the informal ideas introduced in these notes fall under that umbrella.}.

And what do we mean by \textbf{causal effects}? ``(...) causal effects in
populations, that is, \textbf{numerical quantities} that measure changes in the
distribution of an outcome under different \textbf{interventions}.'' \citep[p.\
v]{hernan2020} (emphasis is mine)


\subsection{There is no such thing as  ``spurious association''. But when people  use this term, it suggests they are trying to obtain causal estimates}

In the above study, there is a possible obvious problem. Suppose you observe an
association between moderate red wine consumption and better cardiovascular
health. Maybe what is happening is that, in the sample you are using, people who
consume moderate amounts of red wine are also people who consume olive oil and
lots of fresh vegetables (the Mediterranean diet?).  The observed association
between red wine consumption and better cardiovascular health is not a causal
association: the association is the result of both red wine consumption and
better cardiovascular health being effects (or consequences) of the type of
diet. But red wine has no direct effect on cardiovascular health (we will see
examples of this pattern below: Figure \ref{dag-structs}). A similar well known
phenomenon is the very real association between ice cream sales and homicide
rates (ice cream sales is positively correlated with homicide rates, at
least in some parts of the world: more ice cream, more homicides).

Some authors would say there is a ``spurious association'' or ``spurious
correlation''\footnote{Instead of ``spurious'' you might read ``illusory'' or
  ``fictitious'' or ``apparent''.} between red wine consumption
and health (or ice creams and homicides). Well, not really: the association is
not spurious. It is quite real. And there is nothing wrong with computing it, nor
is there anything false, invalid, or fake with it showing up as
positive\footnote{This point is emphasized, for example, by  \citet[][section 7.1]{hernan2020} or \citet{sober2024}}. But the association is not causal.

And the reason we can tell ``there is something wrong going on here if we infer
an effect of red wine on health'' is, precisely, because we are trying to use a
model that has causal interpretations. We are trying to answer questions such as
``Is red wine really good for your health?''  or ``Is switching from not
consuming red wine to consuming moderate amounts of it a good idea?''. See
\citet[][p.\ 84, for similar comments]{hernan2020}


So someone using expressions like ``spurious associations'' is actually revealing
that they really want to say something about causes and effects.


\activities Think of at least two examples, ideally at least one related to your
own research, where you might have thought of ``spurious associations''.


\subsection{What should you read of this long pdf?}\label{whattoread}
I expect you to read all of it, except the Appendix. You can read section
\ref{modified-basic} very, very quickly, except for structure f). The main
objective of this document is to allow you to understand why we should or
shouldn't adjust for covariates in the examples we give (\ref{chol-exercise},
\ref{fungus-ex}, \ref{fungus-collider}, \ref{pretreat-no},
\ref{cause-of-cause}, \ref{amplification}, \ref{bwparadox}).

Sections \ref{dag-structs}, \ref{backdoor-basics} are there just to explain why.

More complex examples are provided in \ref{direct-indirect}, but you can skip
this if you want.

The Appendix (section \ref{appendix}) is optional (though not harmful).

<<load_libs, echo=FALSE, results='hide',message=FALSE>>=
## Plots, with dagitty
library(dagitty)

## library(rethinking) ## for drawdag
## Installing rethinking can be complicated just for a few graphs
## So have a fallback if rethinking not available
if(!suppressWarnings(require("rethinking", quietly = TRUE))) {
    drawdag <- plot
}

library(car)
@

\section{Graphs, DAGs, notation}

Graphs, such as the one in Figure \ref{fig:plot_dag_1}, are very useful to represent
causal concepts. In that figure, Age is a \textbf{common cause} of Exercise and
Cholesterol, and Exercise has a direct effect on Cholesterol too.  These are
\textbf{DAG}s, for Directed Acyclic Graphs; Directed because there is direction, and thus we see arrows,
not just edges; Acyclic because there are no cycles: you do not go through a variable twice if you follow arrows.

% (Yes, we do know that we should recommend people exercise if they want to lower
% their cholesterol)

<<dag_1, results='hide', echo=FALSE>>=
common_cause <- dagitty("dag {
Age -> Exercise
Age -> Cholesterol
Exercise -> Cholesterol
}")

@



%% <<plot_dags_1_2, out.width = '14cm', out.height='7cm'>>=
<<plot_dag_1, fig.width = 4, fig.height=2, fig.lp='fig:', results = 'hide', echo=FALSE, fig.align = 'center', fig.cap='Cholesterol, Exercise, Age example',out.width='10cm', fig.pos="!h">>=
coordinates(common_cause) <- list(x = c(Exercise = 1, Age = 2, Cholesterol = 3),
                                  y = c(Exercise = 0, Age = -1, Cholesterol = 0))

drawdag(common_cause, xlim = c(0.5, 3.5), ylim = c(0, 1.3))
## text(x = 2, y = 1.2, labels ="a)", cex = 1.2)

@

Sometimes we will use variables denoted as  $U$ (or $U$ with subindices): these
are unobserved variables.

% Total, direct and indirect effect

\activities Draw a DAG for the wine, diet, cardiovascular health example
discussed before.

\section{An introductory example of adjusting for covariates that are common
  causes: Cholesterol, Exercise, Age}\label{chol-exercise}


Suppose we sample subjects from a population where, as people get older, they
both exercise more and have higher cholesterol levels. At the same time, for a
given age, the more people exercise, the lower their cholesterol level.  Given a
sample of data where we have collected age, exercise patterns, and cholesterol
levels, how should we analyze the data? (This example is taken from chapter 1,
pp.\ 3 to 5, of \citealp{pearl_causal_2016}). The relationships between the
variables are shown in Figure \ref{fig:plot_dag_1}.





Here I simulate some data that follow the above relationships.

<<simul_1, results='hide', echo = TRUE>>=
N <- 1e4
################## Common_cause
common_cause <- data.frame(Age = rnorm(N, 30, 5))
common_cause$Exercise <- 2 * common_cause$Age + rnorm(N)
common_cause$Cholesterol <- 3 * common_cause$Age -
  common_cause$Exercise +
  rnorm(N)

@


Before turning the page, think what kind of relationship you expect between
Cholesterol and Exercise in the whole population and between Cholesterol and Exercise for people of age 10, and for people of age 20, \ldots.

\clearpage
The process above generate data that look like this:


\begin{figure}[h!]
  \centering
  \begin{minipage}{0.45\textwidth}
        \centering
        \includegraphics[width=0.9\textwidth]{chol-ex1-crop}% first figure itself
%       \caption{first figure}
    \end{minipage}\hfill
    \begin{minipage}{0.45\textwidth}
        \centering
        \includegraphics[width=0.9\textwidth]{chol-ex2-crop} %second figure itself
%       \caption{second figure}
    \end{minipage}
  % \includegraphics[width=0.50\paperwidth,keepaspectratio]{chol-ex1.pdf}
  % \includegraphics[width=0.50\paperwidth,keepaspectratio]{chol-ex2.pdf}
   \caption{\label{fig:chol-exercise-pearl-et-al} Relationships between
     Cholesterol and Exercise, by age and over the complete population. From
     \citet{pearl_causal_2016}, Figures 1.1. and 1.2 (which are the same as
     Figure 6.6 in \citealp{pearl2018}; a preview of chapter 1 of
     \citealp{pearl_causal_2016} is available from Pearl's page: \Burl{http://bayes.cs.ucla.edu/PRIMER/}). }
\end{figure}


\clearpage
Let's analyze the data with and without adjusting for Age.


<<code_1, results='show', echo = TRUE>>=
m_common_cause_adjust <- lm(Cholesterol ~ Exercise + Age,
                            data = common_cause)
m_common_cause_no_adjust <- lm(Cholesterol ~ Exercise,
                               data = common_cause)

## Function "S" is from the car library
S(m_common_cause_adjust)
S(m_common_cause_no_adjust)
@



We must adjust (or control) for Age, the common cause of Exercise and Age: if we
don't adjust for Age, the estimate of the effect of Exercise on Cholesterol is
confounded by Age having effects on both Exercise and
Cholesterol\footnote{When dealing with categorical variables, this pattern,
  where the association of two variables changes, or even reverts its sign, when
  we account for another, is also called Simpson's paradox.}. Age is a
\textbf{confounder}. And notice that ``confounder'' is something we define with respect to measuring causal effects, so the causal perspective is essential for identifying (and correcting for) confounders\footnote{Pearl elaborates on this at length, when he discusses the so-called ``Simpson's paradox'': it only seems paradoxical when viewed purely as a statistical phenomenon, without causal reasoning.}.


% : there is \textbf{confounding} due to Age in the estimate of
% the effect of Exercise on Cholesterol.

% Or, unless we adjust for Age, there will be \textbf{confounding}: the
% true causal relationship (or its absence) between Exercise and Cholesterol will
% be confounded by Cholesterol and Exercise both having Age as a common cause.



%% FIXME: maybe this lesson after the one on chi-squares?



\section{Should we always adjust for covariates? Fungus and the post-treatment variable}
\label{fungus-ex}


The following example is modified from \citet[][pp.\
170--174]{rethinking_2020}. An experiment is conducted to asses the effects of an
antifungal treatment (Treatment) on plant final size (Size). The amount of fungus
(a post-treatment variable, Fungus) is also measured. Since plots varied in
quality, in ways that could affect final plant Size, a variable (or variables)
Plot measure the plot quality (pretreament, though this is irrelevant since this
variable, or variables, are not affected by treatment). The DAG is shown in Fig.~\ref{fig:plot_fungus_1}.

<<dag_fungus_1, results='hide', echo=FALSE>>=
fungus1 <- dagitty("dag {
Treatment -> Fungus
Fungus -> Size
Plot -> Size
}")

@

<<plot_fungus_1, fig.width = 4, fig.height=1.4, fig.lp='fig:', results = 'hide', echo=FALSE, fig.align = 'center', fig.cap='Fungus, first example',out.width='9cm', fig.pos="!h">>=
coordinates(fungus1) <- list(x = c(Treatment = 1, Fungus = 2,
                                        Plot = 2.5,
                                        Size = 3),
                                  y = c(Treatment = -0.5, Fungus = 0,
                                        Plot = -1,
                                        Size = 0))

drawdag(fungus1, xlim = c(0.5, 3.5), ylim = c(-.1, 1.3))
## text(x = 2, y = 1.2, labels ="a)", cex = 1.2)

@


%% Write R code for this!

We definitely want to adjust for Plot to reduce the variability in our
estimates.

What about Fungus: no, we do not want to adjust for it, as adjusting
for Fungus would actually prevent us from estimating the effect of Treatment:
Treatment affects plant size through Fungus. Once we know about Fungus, Treatment
says nothing about Size \footnote{Size is conditionally independent of Treatment
  given Fungus, $Size \upmodels Treatment | Fungus$. The  $\upmodels$ symbol
  means independence. You can ignore this notation if it does not help you.

  You might also read the expression ``Fungus screens-off Size from Treatment'': \(P(S|F \& T) = P(S|F) \ne P(S|T)\), where \(S, F, T\) denote Size, Fungus, Treatment, respectively; the ``screening-off'' expression is common in the philosophical literature.}.



Even if the true relationship was as shown in Figure \ref{fig:plot_fungus_2} we would not
want to use Fungus as a covariate. Here Treatment is not independent of Size
given Fungus, but Fungus mediates in the relationship. If we added Fungus in the
statistical model, we would not be estimating the total effect of Treatment on
Size (if you want more details, go to Appendix, \qref{direct-indirect}).



<<dag_fungus_2, results='hide', echo=FALSE>>=
fungus2 <- dagitty("dag {
Treatment -> Fungus
Treatment -> Size
Fungus -> Size
Plot -> Size
}")

@

<<plot_fungus_2, fig.width = 4, fig.height=1.4, fig.lp='fig:', results = 'hide', echo=FALSE, fig.align = 'center', fig.cap='Fungus, second example',out.width='9cm',fig.pos="!h">>=
coordinates(fungus2) <- list(x = c(Treatment = 1, Fungus = 2,
                                        Plot = 2.5,
                                        Size = 3),
                                  y = c(Treatment = -0.5, Fungus = 0,
                                        Plot = -1,
                                        Size = 0))

drawdag(fungus2, xlim = c(0.5, 3.5), ylim = c(-.1, 1.3))
## text(x = 2, y = 1.2, labels ="a)", cex = 1.2)

@


\section{More fungus: a collider}\label{fungus-collider}

This example is modified from \citet[][p.\ 175]{rethinking_2020}. Suppose
now that Fungus does not affect final Size. But both Fungus  and Size are
affected by moisture (moisture and Plot quality are different
variables). Moreover, and this is crucial, moisture has not been measured, so
there is no way for you to adjust for it, and it is shown as U in the DAG below,
Figure \ref{fig:fungus_collider}.


<<dag_fungus_3, results='hide', echo=FALSE>>=
fungus3 <- dagitty("dag {
Treatment -> Fungus
U -> Fungus
U -> Size
Plot -> Size
}")

@

<<fungus_collider, fig.width = 4, fig.height=1.4, fig.lp='fig:', results = 'hide', echo=FALSE, fig.align = 'center', fig.cap='Fungus, collider example',out.width='9cm',fig.pos="!h">>=
coordinates(fungus3) <- list(x = c(Treatment = 1,
                                   Fungus = 2,
                                   Plot = 1,
                                   U = 1,
                                   Size = 3),
                             y = c(Treatment = -1.5,
                                   Fungus = -1,
                                   Plot = 0,
                                   U = -0.5,
                                   Size = 0))

drawdag(fungus3, xlim = c(0.5, 3.5), ylim = c(-.1, 1.6))
## text(x = 2, y = 1.2, labels ="a)", cex = 1.2)

@

In Figure \ref{fig:fungus_collider}, Fungus is a descendant of both U and
Treatment. This is called a \textbf{collider}. Conditioning on Fungus will lead
to Treatment and moisture (U) being associated, even when they are really
independent of each other. And that would lead to our mistakenly estimating that
Treatment has an effect on Size (U affects Size and U is associated with
Treatment when we condition on Fungus), when Treatment really does not have an
effect on Size.

OK, this is getting complicated. Let us see the three basic DAG structures,
and a few derived ones.


(But before we leave this example: what should we have done? Include in the model
Treatment, which is the variable we are interested in, and also Plot, to decrease
variability of the estimates. If we could have adjusted for U, we would have adjusted for it, but we can't adjust for U; anyway, not including U in the model will increase
the variability, but will not lead to bias. The bad idea was adjusting for
Fungus.)

\clearpage
\section{Basic DAG structures}\label{dag-structs}

\subsection{The three basic DAG structures}\label{three-basic-structs}
The basic DAG structures with their names\footnote{This is fairly standard material; you can find it in,
for example, Figure 3.3 in \citet{morgan_counterfactuals_2015}, section 6.3 in
\citet{hernan2020}, sections 2.2. and 2.3 in \citet{pearl_causal_2016}, Figure
8.1 in \citet{kline2015}.} are presented in Figure
\ref{fig:plot_dag_struct}.




<<dag_struct, results='hide', echo=FALSE>>=
chain <- dagitty("dag {
X -> Z
Z -> Y
}")

fork <- dagitty("dag {
Z -> X
Z -> Y
}")

collider <- dagitty("dag {
X -> Z
Y -> Z
}")

@

<<plot_dag_struct, fig.width = 5, fig.height=2.5, fig.lp='fig:', results = 'hide', echo=FALSE, fig.align = 'center', fig.cap='Basic DAG structures',out.width='14cm',fig.pos="!h">>=
op <- par(mfrow = c(1, 3))

coordinates(chain) <- list(x = c(X = 1,
                                 Y = 3,
                                 Z = 2),
                           y = c(X = 0,
                                 Y = 0,
                                 Z = 0))

coordinates(fork) <- list(x = c(X = 1,
                                 Y = 3,
                                 Z = 2),
                           y = c(X = 0,
                                 Y = 0,
                                 Z = -.50))

coordinates(collider) <- list(x = c(X = 1,
                                 Y = 3,
                                 Z = 2),
                           y = c(X = -.5,
                                 Y = -.5,
                                 Z = 0))



drawdag(chain, xlim = c(0.5, 3.5), ylim = c(-1, 1.3))
text(x = 2, y = -.4, labels ="a) Chain.\n Z mediates", cex = 1.1)


drawdag(fork, xlim = c(0.5, 3.5), ylim = c(-1, 1.3))
text(x = 2, y = -.4, labels ="b) Fork.\n Z common cause", cex = 1.1)


drawdag(collider, xlim = c(0.5, 3.5), ylim = c(-1, 1.3))
text(x = 2.1, y = -.4, labels ="c) Inverted fork with collider.\n Z common effect: collider", cex = 1.1)

@


Each of those structures determines the pattern of association between variables.
For example, in the Chain case, we know that X causes Z that causes Y. Those are
the causal relationships. Now, what \textbf{associations} will we observe? You
can think of the DAGs as pipes, and association flows (or not) through these
pipes (see \citealp[][ch.~6]{hernan2020}; in Miguel Hern\'an's edX
course ``Causal Diagrams: Draw Your Assumptions Before Your Conclusions''\\
\Burl{https://www.edx.org/course/causal-diagrams-draw-your-assumptions-before-your},
you can see animations of this process).  Both a mediator and a common cause, if
conditioned upon, block the flow of information because they close the pipe; in
contrast, a collider, if conditioned upon, opens the pipe. Make sure to play with the analogy of the pipe, and apply it to the figures, thinking about the effect of closing an imaginary tap in Z.

Let us reword the above. In the chain example in Figure \ref{fig:plot_dag_struct} a),
if we do not condition in Z, the pipe is open, so X and Y are
associated\footnote{Strictly: ``are very likely associated'' as it could happen
  that they are not, but this would be rare.}. But if we condition on Z, we close
the pipe, the flow of association, and now X and Y are conditionally independent
given Z. The same thing happens in Figure \ref{fig:plot_dag_struct} b). But the
opposite thing happens in Figure \ref{fig:plot_dag_struct} c).



More systematically:
\begin{enumerate}[label=\alph*)]

\item Chain: X and Y are associated. But conditioning on Z will render X and Y
  independent (there will be no association). The conditional and unconditional
  dependencies are (you can ignore this if it does not help you):
  $X \upmodels Y \ | \ Z$, \quad $X \nupmodels Y$.



\item Fork: X and Y are associated. But conditioning on Z will render X and Y
  independent (there will be no association). $X \upmodels Y\ | \ Z$, \quad
  $X \nupmodels Y$. %%$X \cancel{\upmodels} Y$

  This is the usual example of \textbf{confounding}, where we see association
  because of a common cause.

\item Inverted fork with collider: X and Y are independent. But conditioning on Z
  will make X and Y associated\footnote{If these were numerical variables and we
    assume a linear model, they would be correlated. Association and
    non-independence are more general concepts than correlation.}:
  $X \nupmodels Y\ | \ Z$, \quad $X \upmodels Y$.


\end{enumerate}


More about \textbf{confounding}. In Figure \ref{fig:plot_dag_struct} b) we must adjust for Z, or condition on Z, to
avoid confounding the estimate of the relationship between X and Y. It is the
presence of confounding that leads to the ``correlation is not necessarily
causation'' \citep[][p.\ 58]{westreich2019}.  (For more details about confounding
see chapter 7 in \citealp{hernan2020}; a brief discussion in section 3.5.1, pp.\
58 and ff., in \citealp{westreich2019})


%% ZZ FIXME : give the example of Y must compensate whatever X has
And more about \textbf{colliders}. The consequences of the last structure, Figure \ref{fig:plot_dag_struct} c), where
we have a collider, sometimes seem counterintuitive. This structure is behind
``Berkson's paradox''\footnote{
  \url{https://en.wikipedia.org/wiki/Berkson\%27s_paradox}, and it might explain
  ``Why are handsome men such jerks?'' ---and, I guess, a similar phenomenon with
  women:
  \url{http://www.slate.com/blogs/how_not_to_be_wrong/2014/06/03/berkson_s_fallacy_why_are_handsome_men_such_jerks.html}
  .}. A simple example: suppose there is no association between bone fracture
and pneumonia in the general population. But if you only look at people who go to
the emergency room in a hospital, you are likely to find a negative association
between pneumonia and bone fracture (think about why people go to hospitals
---there must be some reason to be in the hospital to begin with, and either
severe pneumonia or a broken bone are enough to take you there).

Another way to understand it: suppose you only look at a value, or small set of
values, of Z (that is what conditioning is); now, if X has any value, the value
of Y has to compensate the value of X, so that the value of Z is the one you
conditioned on.


If these examples are not clear, look at the Wikipedia entry linked in the
footnotes (or the ``Why are handsome men such jerks'', linked in the footnote
too). Conditioning (and restricting) on colliders leads to \textbf{selection
  bias} (see chapters 7 and 8 in \citealp{hernan2020}, and a brief account in
section 3.5.3, pp.\ 64--66 in \citealp{westreich2019})

\activities: Think of at least one example for each of the structures
above. \textbf{Really, do it}. Ideally, think of two examples, one from
``everyday life'' and one from you scientific work/TFM/etc.


\subsection{Terminology: ``condition on'', ``given'', ``adjusting for''}\label{condition-given}
The following three expressions are equivalent, and you will find them in the literature:
\begin{itemize}
\item X and Y are independent \textit{given} Z.
\item X and Y are independent \textit{if we condition on} Z (or
  \textit{conditioning on} Z).
\item X and Y are independent \textit{if we adjust for} Z (or \textit{adjusting
    for} Z).\footnote{X and Y are independent \textit{if we hold Z constant} can
    be equivalent, though this is not as common as the above expressions with
    ``condition on'', ``given'', ``adjusting'', and we would need to be more
    precise about the meaning of \textit{holding constant}: are we really,
    physically holding Z constant via intervention, or adjusting statistically
    for it, as in conditioning?}
\end{itemize}


\subsection{Descendants and ancestors in the basic DAG structures}\label{modified-basic}

To make sure we understand how the flow of association is blocked or unblocked,
let us add some descendants and ancestors to the previous structures and see what
happens. If you want, you can read this section very quickly and skip over all
the ``in addition''. The \textbf{most important structure to pay attention to is
  f)}. The rest are here for completeness, but following it actually only requires
to use the rules we have explained above.


We have modified the basic structures as follows:
\begin{itemize}
\item In the top row, we have added a descendant of Z
\item In the bottom row, we have added an ancestor of Z
\end{itemize}

<<dag_struct2, results='hide', echo=FALSE>>=
c1 <- dagitty("dag {
X -> Z
Z -> Y
Z -> W
}")

c2 <- dagitty("dag {
X -> Z
Z -> Y
W -> Z
}")


f1 <- dagitty("dag {
Z -> X
Z -> Y
Z -> W
}")


f2 <- dagitty("dag {
Z -> X
Z -> Y
W -> Z
}")


co1 <- dagitty("dag {
X -> Z
Y -> Z
Z -> W
}")

co2 <- dagitty("dag {
X -> Z
Y -> Z
W -> Z
}")

@

<<plot_dag_struct2, fig.width = 5, fig.height=4.5, fig.lp='fig:', results = 'hide', echo=FALSE, fig.align = 'center', fig.cap='Descendants and ancestors in the basic DAG structures',out.width='12cm'>>=
op <- par(mfrow = c(2, 3))

coordinates(c1) <- list(x = c(X = 1,
                              Y = 3,
                              Z = 2,
                              W = 2),
                        y = c(X = 0,
                              Y = 0,
                              Z = 0,
                              W = -0.5))

coordinates(c2) <- list(x = c(X = 1,
                              Y = 3,
                              Z = 2,
                              W = 2),
                        y = c(X = 0,
                              Y = 0,
                              Z = 0,
                              W = -.5))


coordinates(f1) <- list(x = c(X = 1,
                              Y = 3,
                              Z = 2,
                              W = 2),
                           y = c(X = 0,
                                 Y = 0,
                                 Z = -.50,
                                 W = -1))


coordinates(f2) <- list(x = c(X = 1,
                              Y = 3,
                              Z = 2,
                              W = 2),
                           y = c(X = 0,
                                 Y = 0,
                                 Z = -.50,
                                 W = -1))



coordinates(co1) <- list(x = c(X = 1,
                              Y = 3,
                              Z = 2,
                              W = 2),
                        y = c(X = -1,
                              Y = -1,
                              Z = -.5,
                              W = 0))



coordinates(co2) <- list(x = c(X = 1,
                              Y = 3,
                              Z = 2,
                              W = 2),
                        y = c(X = -1,
                              Y = -1,
                              Z = -0.5,
                              W = 0))


drawdag(c1, xlim = c(0.5, 3.5), ylim = c(-1, 1.3))
text(x = 2, y = -.4, labels ="d)", cex = 1.4)

drawdag(f1, xlim = c(0.5, 3.5), ylim = c(-1, 1.3))
text(x = 2, y = -.4, labels ="e)", cex = 1.4)

drawdag(co1, xlim = c(0.5, 3.5), ylim = c(-1, 1.3))
text(x = 2, y = -.4, labels ="f)", cex = 1.4)


drawdag(c2, xlim = c(0.5, 3.5), ylim = c(-1, 1.3))
text(x = 2, y = -.4, labels ="g)", cex = 1.4)

drawdag(f2, xlim = c(0.5, 3.5), ylim = c(-1, 1.3))
text(x = 2, y = -.4, labels ="h)", cex = 1.4)

drawdag(co2, xlim = c(0.5, 3.5), ylim = c(-1, 1.3))
text(x = 2, y = -.4, labels ="i)", cex = 1.4)

@




These are the consequences:
\begin{enumerate}[label=\alph*)]
  \setcounter{enumi}{3}
\item Conditioning on W does not make X and Y independent, so X and Y are still
  associated if you condition on W\footnote{If you cannot
    measure Z, but you can measure W, and W and Z are very strongly associated,
    conditioning on W can help you remove some bias if you need to make X and  Y
    conditionally independent. This is more advanced material.}.  Why? Because the flow through Z has not been
  interrupted.

  In addition (but this is not new):
  \begin{enumerate}[label=\arabic*.]
  \item X and W are associated.
  \item Y and W are associated.
  \item X and W are independent if we condition on  Z.
  \item Y and W are independent if we condition on Z.
  \end{enumerate}
  % $X \nupmodels Y | W$.

\item As above: conditioning on W does not make X and Y independent.

  In addition (but this is not new):
  \begin{enumerate}[label=\arabic*.]
  \item X and W are associated.
  \item Y and W are associated.
  \item X and W are independent if we condition on Z.
  \item Y and W are independent if we condition on Z.
  \end{enumerate}
  % $X
  % \nupmodels Y | W$.

\item \textbf{Pay attention here}: conditioning on W will make X and Y
  associated. This is the general rule: \textbf{conditioning on a collider} (as
  in c)) or \textbf{a descendant of a collider will make the ancestors
    associated}. Why? Think about the hospital, broken bones and pneoumonia;
  instead of looking at people at the door of the hospital you look at people
  downstream (e.g., people who have been admitted to the hospital). Or think again about the pipes: put a tap on W, and close it.

  In addition (but this is not new):
  \begin{enumerate}[label=\arabic*.]
  \item X and W are associated.
  \item Y and W are associated.
  \item X and W are independent if we condition on Z.
  \item Y and W are independent if we condition on Z.
  \end{enumerate}
  % $X
  % \nupmodels Y | W$ (and $X
  % \nupmodels Y | Z$,  \quad $X \upmodels
  % Y$).

\item Conditioning on W will not render X and Y independent. Notice also that \textbf{now Z is
  a collider with respect to X and W}. So conditioning on Z will induce an
association between X and W.

In addition:
  \begin{enumerate}[label=\arabic*.]
  \item X and W are independent.
  \item Y and W are associated.
  \item X and W are associated if we condition on Z (we just said this).
  \item Y and W are independent if we condition on Z.
  \end{enumerate}

\item Conditioning on W will not render X and Y independent.

  In addition:
  \begin{enumerate}[label=\arabic*.]
  \item X and W are associated.
  \item Y and W are associated.
  \item X and W are independent if we condition on Z.
  \item Y and W are independent if we condition on Z.
  \end{enumerate}


\item Now Z is a collider with respect to all three variables X, Y, W.
  \begin{enumerate}[label=\arabic*.]
  \item X and Y are independent (we saw this before).
  \item X and W are independent.
  \item Y and W are independent.
  \item X and W are associated if we condition on Z (Z is a collider).
  \item Y and W are associated if we condition on Z (Z is a collider).
  \item X and Y are associated if we condition on Z (Z is a collider), as it was before.
  \end{enumerate}


\end{enumerate}


\activities Go back to the examples (\qref{chol-exercise}, \qref{fungus-ex},
\qref{fungus-collider}): it should now be clear why we should/should not adjust
for the different variables (i.e., pay attention to whether they are common
causes, mediators, or colliders).

\clearpage
\section{A systematic procedure to find what variables to condition on. An
  overview of the backdoor criterion}
\label{backdoor-basics}
% \subsection{The backdoor criterion: basics}
Is there a systematic way to find what variables we should condition on when we
want to estimate the causal effect of X on Y, and avoid being confounded? Yes,
there is. The key ideas are:
\begin{itemize}
\item Block all paths that induce a non-causal association between X and Y (such
  as those created by common ancestors).
\item Do not block directed paths between X and Y (those that are legitimate
  causal connections from X to Y) that would ``rob'' some of the true causal flow.
\item Do not create associations between X and Y by conditioning on colliders or
  descendants of colliders.
\end{itemize}

And this can be done using a systematic procedure. In the appendix, \qref{backdoor-crit}, I give the
 procedure in full detail.




% \subsection{Variance and bias, or random and systematic error}
% Westreich, pp. 24 and 25. (relationship to notions of validity and precision,
% though I prefer to use bias and variance)

% Bias: ``sesgo'', in Spanish


\clearpage
\section{Additional examples}\label{add-examples}

\subsection{A pretreatment collider variable we should not adjust on}\label{pretreat-no}
Suppose the relationships in Figure \ref{fig:plot_dag_ptr} (from Figure 18.6,
section 18.2, p.\ 227 in \citealp{hernan2020}), and you are interested in the
effect of X on Y ($U_1$ and $U_2$ are two different unmeasured variables). Should
you adjust for L, which is a pre-treatment variable?


<<dag_ptr, results='hide', echo=FALSE>>=
ptr <- dagitty("dag {
X -> Y
U_1 -> L
U_2 -> L
U_1 -> Y
U_2 -> X
}")
@

<<plot_dag_ptr, fig.width = 4, fig.height=2.73, fig.lp='fig:', results = 'hide', echo=FALSE, fig.align = 'center', fig.cap='A pretreatment collider.',out.width='9cm', fig.pos= "!h">>=
coordinates(ptr) <- list(x = c(L = 1, X = 2, Y = 3, U_1 = 0.8, U_2 = 0.8),
                         y = c(L = 0, X = 0, Y = 0, U_1 = -.5, U_2 = .5))

drawdag(ptr, xlim = c(0.5, 3.5), ylim = c(-.51, .6))
## text(x = 2, y = 1.2, labels ="a)", cex = 1.2)
@


(To turn the above into a specific example:

<<dag_ptr22, results='hide', echo=FALSE>>=
## ptr22 <- dagitty("dag {
## Diet -> Outcome
## U_g -> Exercise
## U_c  -> Exercise
## U_g -> Outcome
## U_c  -> Diet
## }")
ptr22 <- dagitty("dag {
Exercise -> Outcome
U_g -> ChildhoodBMI
U_c  -> ChildhoodBMI
U_g -> Outcome
U_c  -> Exercise
}")
@

<<plot_dag_ptr22, fig.width = 4, fig.height=2.73, fig.lp='fig:', results = 'hide', echo=FALSE, fig.align = 'center', fig.cap='A pretreatment collider; Uc: country, Ug: genetics.',out.width='9cm', fig.pos= "!h">>=
## coordinates(ptr22) <- list(x = c(Exercise = 1, Diet = 2,
##                                  Outcome = 3,
##                                  U_g = 0.8,
##                                  U_c = 0.8),
##                            y = c(Exercise = 0,
##                                  Diet = 0,
##                                  Outcome = 0,
##                                  U_c = .5,
##                                  U_g = -.5))

coordinates(ptr22) <- list(x = c(ChildhoodBMI = 1,
                                 Exercise = 2,
                                 Outcome = 3,
                                 U_g = 0.8,
                                 U_c = 0.8),
                           y = c(ChildhoodBMI = 0,
                                 Exercise = 0,
                                 Outcome = 0,
                                 U_c = .5,
                                 U_g = -.5))


drawdag(ptr22, xlim = c(0.5, 3.5), ylim = c(-.51, .6))
## text(x = 2, y = 1.2, labels ="a)", cex = 1.2)
@

)


You know the answer. No, do not adjust for L (Childhood BMI): it is a collider ($U_1$ and $U_2$
are its parents) on the backdoor path between X and Y. If we adjust for L, it
will induce a non-causal association between X and Y\footnote{The bias induced is
  sometimes called \textit{M-bias}.}.


Main moral of this story: \textbf{adjusting for all possible pre-treatment
  variables is not always a good idea}. More on that below.


Another moral of the story: \(U_c\) might not be an unmeasured variable. Maybe it is there, in the dataset, but you have not used it. If you were to include it in your model, then we would have blocked the backdoor path.

Still, the main moral of this story remains: \textbf{adjusting for all possible pre-treatment
  variables is not always a good idea}.




\subsection{Should we adjust for the cause of the cause?}\label{cause-of-cause}

Suppose the relationships in Figure \ref{fig:plot_dag_zxy}, and you are
interested in the effect of X on Y. Should you adjust for Z?


<<dag_zxy, results='hide', echo=FALSE>>=
ccc <- dagitty("dag {
Z -> X
X -> Y
}")
@

<<plot_dag_zxy, fig.width = 4, fig.height=.5, fig.lp='fig:', results = 'hide', echo=FALSE, fig.align = 'center', fig.cap='Cause of a cause.',out.width='8cm', fig.pos= "!h">>=
coordinates(ccc) <- list(x = c(Z = 1, X = 2, Y = 3),
                         y = c(Z = 0, X = 0, Y = 0))

drawdag(ccc, xlim = c(0.5, 3.5), ylim = c(-.051, .051))
## text(x = 2, y = 1.2, labels ="a)", cex = 1.2)
@


Short answer: no. If you do, it will increase the noise of the estimate of the
effect of X on Y. It will not introduce bias, but it will increase the standard
error of the estimated effect. (Code to see how adjusting for Z leads to
increased variability of the estimates is provided in file
\texttt{Z\_X\_Y\_adjust\_Z.R}, in the repo.)

Longer answer: no, but sometimes people adjust for Z because Z might be a common
cause of X and Y. Here the argument is ``if I do not adjust for Z and Z is a
common cause of X and Y, it will introduce bias that will result in possibly very
serious confounding. If I adjust for Z when Z is just the cause of X what will
happen is that the standard error of the estimate of X on Y will increase, but
there will be no bias''. That is a possibly sensible argument.


Is there a way to decide? Yes, it might be possible to examine if you really need
to adjust for Z and, then, avoid adjusting for Z. See \citet{vanderweele2011},
section 4 (p.\ 1409, and p.\ 1411 with the results of their simulations).

\subsection{The cause of the cause and bias amplification}\label{amplification}

Now consider the DAG (U is an unmeasured variable) in Figure \ref{fig:plot_dag_bias_amp}:

<<dag_bias_amp, results='hide', echo=FALSE>>=
bamp <- dagitty("dag {
Z -> X
X -> Y
U -> X
U -> Y
}")
@

<<plot_dag_bias_amp, fig.width = 4, fig.height=1.5, fig.lp='fig:', results = 'hide', echo=FALSE, fig.align = 'center', fig.cap='Cause of a cause and bias amplification.',out.width='8cm', fig.pos= "!h">>=
coordinates(bamp) <- list(x = c(Z = 1, X = 2, Y = 3, U = 1),
                         y = c(Z = 0, X = 0, Y = 0, U = -.5))

drawdag(bamp, xlim = c(0.5, 3.5), ylim = c(0, .9))
## text(x = 2, y = 1.2, labels ="a)", cex = 1.2)
@

Adjusting for Z is generally a very bad idea here, because it can lead to
\textbf{bias amplification}: amplification of the bias induced by U. Of course,
things would be OK if you could adjust for U (but U has not been measured).
More details in section 18.2, pp.\ 224 and ff.\ of \citet{hernan2020}; this
phenomenon is also mentioned in \citet{vanderweele2011}\footnote{Actually, Z
could be used as an instrument, or instrumental variable, but when adjusting for
it, Z is not being used as an instrument. Instrumental variables are frequently used in causal inference in economics and sociology; see \citet{morgan_counterfactuals_2015} for many examples and details.}.

\subsection{A more complex, but very real, example: the birth-weight paradox}\label{bwparadox}

The ``birth weight paradox'' is explained in detail in
\citet{hernandez-diaz2006}. The Wikipedia has it under the name ``Low
birth-weight paradox''
(\Burl{https://en.wikipedia.org/wiki/Low_birth-weight_paradox}). This is an issue
of major practical relevance that, if poorly analized and understood, could lead
to harmful recommendations.

I copy from p.\ 1115 of \citet{hernandez-diaz2006}:

\begin{quoting}
  Low birth weight (LBW) infants in groups with a high prevalence of LBW have a
  lower mortality rate than LBW infants in groups with a low prevalence of LBW,
  whereas the opposite is true for normal-weight infants. (...)

  For example, when studies compared mortality rates between LBW infants born to
  smokers and nonsmokers, infants of smokers had lower mortality rates.

  Although it is widely accepted that infants born to mothers who smoke have
  lower birth weights and are at higher risk of neonatal mortality, it has been
  suggested that the effect of maternal smoking is modified by birth weight in
  such a way that smoking is beneficial for LBW babies.
\end{quoting}

(Does the above sound confusing? It was for me. Write, with your own words and your own pencil, a simple scheme of what is being described.)


This is another case of collider bias, in this case stratifying on a common
effect. In Figure \ref{fig:bw-paradox} there are two possible causal DAGs that
would lead to this paradox.

\begin{figure}[h!]
  \centering
  \includegraphics[width=0.9\textwidth]{bw-paradox-1-crop}
  \centering
  \includegraphics[width=0.9\textwidth]{bw-paradox-2-crop}
  \caption{\label{fig:bw-paradox}. Two DAGs that would result in the
    birth-weight paradox. From Figure 3 in \citet{hernandez-diaz2006}. The
    presence or not of an arrow from LBW to Mortality is not the relevant feature.}
\end{figure}


And what is U and what is an intuitive explanation of this phenomenon? Low birth
weight can be caused by medical conditions other than smoking. Once we know a
baby has low birth weight, if we know it is the child of a smoking mom, then it
is less likely that the baby has those other conditions (this is the usual
``explaining away'' of colliders; see the section where we discussed colliders,
Berkson's paradox, and dating men who are handsome jerks ---section
\ref{dag-structs}). In fact, we do not need LBW to have any effect on
mortality. Look at the last DAG in Figure \ref{fig:bw-paradox}: Smoking is
harmful, but (as explained in the Wikipedia) other causes of low birth weight can
be more harmful than smoking. Thus, among LBW babies, those from smoking moms
show lower death rates. But telling pregnant women to smoke would be a very bad
idea.


Again, the moral of the story is: do not adjust for covariates just because they
have been measured \citep{hernandez-diaz2006a}.


% \subsection{More examples}\label{more-examples}
% Chapter 18 in \citet{hernan2020} contains several examples where the usual
% heuristic procedures for what to include, or not, in a model, fail.


\section{How is all of this relevant if I only do experimental/observational
  work?}
\subsection{Relevance}\label{relevance2}
If your work involves observational data, and you want to interpret the estimates
from your analyses as measures of effect, this is obviously relevant (this is
what all the examples here show \smiley{}).

If you only do experimental work, often you will want to adjust for additional
covariates and, then, knowing what covariates to use becomes crucial if you want
to correctly interpret the effects from your experimental manipulations. Moreover,
causal inference from experimental data arguably makes use of counterfactuals
(see \qref{counterf}).

And regardless of whether you work with observational or experimental data, the causal framework is the appropriate framework to think about confounding, as we have seen above. This cannot be emphasized strongly enough, and if you have doubts, look at the example in \qref{pretreat-no}.


\subsection{But I need to know at least something about the phenomenon I am
  dealing with to do any of this!!!!}\label{need-know}
Well, yes, of course you do. As Miguel Hern\'an emphasized in his edX
course ``Causal Diagrams: Draw Your Assumptions Before Your Conclusions''\\
\Burl{https://www.edx.org/course/causal-diagrams-draw-your-assumptions-before-your},
you have to draw your assumptions before your conclusions.

Causal claims are much stronger than claims about association. They require
making stronger assumptions.

(By the way, we have not touched at all here on topics such as trying to measure
the causes of an effect and finding \textbf{sufficient causes}, nor on trying to
find the causal DAGs from a set of data. We have focused ``just'' on measuring
the effects of causes. For more on those topics, go to \citealp{hernan2020};
\citealp{morgan_counterfactuals_2015}; \citealp{neal_causality_2020}, \citealp{peters2017}).

%% ZZ FIXME  what variables to add to a DAG

\noindent\rule{\textwidth}{1pt}
\clearpage
\setcounter{part}{1}
\part{Appendix and additional material}\label{appendix}
As it says: what follows gives additional details on some issues above. This is \textbf{not} required reading.



\section{Direct and indirect effects}\label{direct-indirect}

\subsection{Estimating direct effects}\label{direct-eff}
Look at the following DAG (this is from section 3.7, pp.\ 75 and ff.\
\citealp{pearl_causal_2016}; a similar example is shown in section 6.3.2, p.\
180--182 of
\citealp{rethinking_2020}\footnote{Though in \citealp{rethinking_2020}, the
  explanation of the problem I find possibly misleading, since the difference
  between the direct and indirect effects is not emphasized enough.}) in Figure \ref{fig:dag_direct}:


<<dag_direct, results='hide', echo=FALSE,fig.width = 4, fig.height=1.7, fig.lp='fig:', fig.align = 'center', fig.cap='Direct effects',out.width='9cm', fig.pos= "!h">>=
op <- par(mfrow = c(1, 2))
dire <- dagitty("dag {
Gender -> Qualification
Gender -> Hiring
Qualification -> Hiring
}")
coordinates(dire) <- list(x = c(Gender = 1, Qualification = 2, Hiring = 3),
                          y = c(Gender = 0, Qualification = -1, Hiring = 0))

drawdag(dire, xlim = c(0.5, 3.5), ylim = c(-.1, 1.3))

## dire2 <- dagitty("dag {
## Exercise -> Food
## Exercise -> Cholesterol
## Food -> Cholesterol
## }")
## coordinates(dire2) <- list(x = c(Exercise = 1, Food = 2, Cholesterol = 3),
##                           y = c(Exercise = 0, Food = -1 Cholesterol = 0))
## drawdag(ptr, xlim = c(0.5, 3.5), ylim = c(-.9, 1.3))
## text(x = 2, y = 1.2, labels ="a)", cex = 1.2)
## par(op)
@

You might want to estimate the \textbf{direct effect} of Gender on Hiring (if
there is any, it could be evidence for discrimination). The direct effect is the
effect not mediated by other variables. In this case, the procedure is simple:
regress Hiring on both Qualification and Gender, and the coefficient for Gender
gives you the direct effect. Why? Because you have removed the effects that go
through Qualification by adding Qualification as a covariate.

The \textbf{total effect} of Gender on Hiring would be obtained by regression
Hiring on Gender (without including Qualification in the model). Total effects
are what we have been mostly concerned with here.


\subsection{Direct effects when there is confounding}\label{direct-eff-conf}

But suppose the way things really are is the one shown in Figure
\ref{fig:dag_direct_conf}, where ``SocioecStatus'' is the socioeconomic status of
the family of the persons being hired (this is from \citealp{pearl_causal_2016}, Fig.~312, p.~77, ---but  I have substituted ``Income'' byt ``SocioecStatus'').

<<dag_direct_conf, results='hide', echo=FALSE,fig.width = 3.5, fig.height=2, fig.lp='fig:', fig.align = 'center', fig.cap='Direct effects and confounding',out.width='8.2cm', fig.pos= "!h">>=
dire3 <- dagitty("dag {
Gender -> Qualification
Gender -> Hiring
Qualification -> Hiring
SocioecStatus -> Qualification
SocioecStatus -> Hiring
}")
coordinates(dire3) <- list(x = c(Gender = 1, Qualification = 2, Hiring = 3,
                                SocioecStatus = 4),
                          y = c(Gender = 0, Qualification = -1, Hiring = 0,
                                SocioecStatus = -1.45))

drawdag(dire3, xlim = c(0.5, 5), ylim = c(-.1, 1.6))
@

If you only adjust by Qualification, your estimates of direct effect will be
biased because Qualification is a collider (a descendant of both SocioecStatus and
Gender). If you wanted an unbiased estimate of the direct effect, you would need
to measure and condition on both Qualification and SocioecStatus.


The estimate of the total effect, where you simply regress Hiring on Gender, in
contrast, will not be biased (and there is no need to measure Qualification or
SocioecStatus).


A structurally similar example is also discussed in ``Technical Point 8.1'', p.\
104, of \citet{hernan2020}, and similar examples in section 8.3.2 and 8.3.3,
pp.\ 280 and ff.\ of \citet{morgan_counterfactuals_2015}. Caveats about the
adjustment of the mediator in the presence of confounding are also given in
\citet{cole2002}, using hypothetical examples from the Physicians' Health
Study. Estimating direct and indirect effects is related to the study of
mediation, and a book-length treatment is \citet{vanderweele2015}.
Finally, for figure \ref{fig:dag_direct_conf}, \citealp{pearl_causal_2016} discuss the difference between conditioning on ``Qualification'' and \textit{fixing it constant} by \textit{intervening} on it, which allows us to compute the \textit{Controlled Direct Effect (CDE)} (the change in Hiring by intervening on both Gender and Qualification, where the presence of SocioecStatus no longer bothers us, since we are manipulation Qualification); we will not discuss this further; \citet{morgan_counterfactuals_2015} explain them in ch.~11, and \citet{hernan2020} on Technical point 22.1 and sections 23.2 and ff.


Of course, you can turn the examples above into a completely different example that could be easier to relate to. For example, with scarce display of imagination on my side:
\begin{itemize}
\item Gender is Gene A, whose expression you can manipulate.
\item Qualification is Gene B
\item SocioecStatus is Gene C
\item Hiring is some desired outcome
\end{itemize}

Please, make this more elaborate (e.g., think about some of the variables above being, say, a particular therapy, etc).



\subsection{Revisiting the fungus example}\label{revisit-fungus}
If you go back to Figure \ref{fig:plot_fungus_2}, doing a regression with Size on
both Fungus and Treatment would be estimating the direct effect of Treatment on
Size. In other words, the coefficient for Treatment would be the direct effect of
Treatment on Size that does not go through (or is not mediated by) the effect of
Fungus on Treatment.

But remember that if there are unmeasured confounders between Fungus and Size, as
we have just seen in the examples above, you can introduce bias.


\subsection{Direct and indirect effects: some R code}\label{direct-indirect-example-R}
In file \texttt{mediator\_cholest\_food\_exercise.R} I present code for an
example similar to the first one. We are interested in the relationship between
Exercise, Cholesterol, and Food consumption.  Even if Exercise directly leads to
a decrease in Cholesterol, Exercise also leads to an increase in Food consumption
and increasing Food consumption (because of the low quality of food available)
leads to an increase in Cholesterol. (This is similar to the example above with
Gender, Hiring, Qualification replaced by, respectively, Exercise, Cholesterol,
Food).  The code in that file shows how adjusting for the mediator gives the
direct effect and how not adjusting for it gives the total effect (for a
model without confounders).


% \subsection{Cholesterol, exercise, food}
% Look now at the relationship depicted in Figure \ref{fig:plot_direct_chol_food}, panel
% ``b)'', and suppose that, even if Exercise directly leads to a decrease in
% Cholesterol, Exercise also leads to an increase in Food consumption and
% increasing Food consumption (because of the low quality of food available) leads
% to an increase in Cholesterol. How would we analyze this data if we want to
% estimate the total effect of Exercise on Cholesterol?



% <<dag_2, results='hide', echo = FALSE>>=
% mediator <- dagitty("dag {
% Exercise -> Food
% Food -> Cholesterol
% Exercise -> Cholesterol
% }")
% @
% %% <<plot_dags_1_2, out.width = '14cm', out.height='7cm'>>=
% <<plot_direct_chol_food, fig.width = 10, fig.height=5, fig.lp='fig:', results = 'hide', echo=FALSE, fig.align = 'center', fig.cap='Introductory figures'>>=
% coordinates(common_cause) <- list(x = c(Exercise = 1, Age = 2, Cholesterol = 3),
%                                   y = c(Exercise = 0, Age = -1, Cholesterol = 0))

% drawdag(mediator, xlim = c(0.5, 3.5), ylim = c(0, 1.3))
% text(x = 2, y = 1.2, labels ="b)", cex = 1.2)
% @


% <<simul_2, results='hide', echo = TRUE>>=
% N <- 1e4

% ################## Mediator
% mediator <- data.frame(Exercise = runif(N, 1, 100))
% mediator$Food <- mediator$Exercise * 3 + rnorm(N)
% ## Cholesterol decreases with Exercise (-1) but increases with Food
% mediator$Cholesterol <- mediator$Food * 2 - mediator$Exercise + rnorm(N)
% @

% And here for case b).
% <<code_2, results='show', echo = TRUE>>=
% m_mediator_adjust <- lm(Cholesterol ~ Exercise + Food, data = mediator)
% m_mediator_no_adjust <- lm(Cholesterol ~ Exercise, data = mediator)

% S(m_mediator_adjust)
% S(m_mediator_no_adjust)

% @

% In case b), if we want to measure the total
% effect of Exercise in this experiment, we should not adjust for Food
% consumption.




\section{Backdoor criterion}\label{backdoor-crit}

Using the backdoor criterion is very well explained in, for example:
\begin{itemize}
\item Section 4.2, pp.\ 109 and ff., of \citet{morgan_counterfactuals_2015} (I
  particularly like how their explanation combines the original Pearl's criterion
  with further generalizations).
\item Section 7.2 and 7.3, pp.\ 85 and ff., of \citet{hernan2020}.
\item Section 3.3, pp.\ 61 and ff., of \citet{pearl_causal_2016}.
\item Section 3.5.1, pp.\ 59 and ff., of \citet{westreich2019}.
\end{itemize}

They are all saying the same thing: how to look for sets of variables that block
what are called backdoor paths.  For completeness, here are full details.


\subsection{Backdoor path}\label{backdoor-path}
The backdoor criterion uses the idea of ``\textbf{backdoor path}'' between two
variables, X and Y. These are two equivalent explanations of what a backdoor path
is:

\begin{quoting}
  (...) a back-door path is defined as any path between the causal variable
  [treatment] and the outcome variable [our Y] that begins with an arrow that
  points to the causal variable
\end{quoting} \citet{morgan_counterfactuals_2015}, Section 1.5, p.\ 30.


\begin{quoting}
In a causal DAG, a
  backdoor path is a noncausal path between treatment [causal variable in
  definition above] and outcome [our Y] that remains even if all arrows pointing
  from treatment to other variables (the descendants of treatment) are
  removed. That is, the path has an arrow pointing into treatment
\end{quoting}
\citet{hernan2020},  Section 7.1, p.\ 83.



\subsection{Using the backdoor criterion}\label{backdoor-criterion-using}


% But we might prefer a less terse explanation.

In section 4.2, pp.\ 109 and ff.,
of \citet{morgan_counterfactuals_2015} the following two-step process is given:

\begin{quoting}
  The overall goal of a conditioning strategy guided by the back-door criterion is to block
all paths that generate noncausal associations between the causal variable and the
outcome variable without inadvertently blocking any of the paths that generate the
causal effect itself. In practice, a conditioning strategy that utilizes the back-door
criterion is implemented in two steps:
\begin{itemize}
\item Step 1: Write down the back-door paths from the causal variable to the
outcome variable, determine which ones are unblocked, and then search
for a candidate conditioning set of observed variables that will block all
unblocked back-door paths.
\item Step 2: If a candidate conditioning set is found that blocks all back-door
paths, inspect the patterns of descent in the graph in order to verify
that the variables in the candidate conditioning set do not block or
otherwise adjust away any portion of the causal effect of interest.\end{itemize}\end{quoting}


\citet{morgan_counterfactuals_2015} then explain in detail
(pp.\ 109 and 110) why that procedure is justified (this is basically Pearl's
backdoor criterion):


\begin{quoting}
  If one or more back-door paths connect the causal variable to the outcome
  variable, the causal effect is identified by conditioning on a set of variables
  $Z$ if

  \begin{itemize}
  \item Condition 1. All back-door paths between the causal variable and
    the outcome variable are blocked after conditioning on $Z$, which
    will always be the case if each back-door path
    \begin{itemize}
    \item (a) contains a chain of mediation $A \rightarrow C \rightarrow B$, where the
      middle variable $C$ is in $Z$, or

    \item (b) contains a fork of mutual dependence $A \leftarrow C \rightarrow B$,
      where the middle variable $C$ is in $Z$, or

    \item (c) contains an inverted fork of mutual causation
      $A \rightarrow C \leftarrow B$, where the middle variable $C$ and all of $C$'s
      descendants are not in $Z$;
    \end{itemize}
    and

  \item Condition 2. No variables in $Z$ are descendants of the causal
    variable that lie on (or descend from other variables that lie on)
    any of the directed paths that begin at the causal variable and
    reach the outcome variable.
  \end{itemize}\end{quoting}


For completeness, here is the backdoor criterion, from section 3.3,
pp.\ 61 and ff.\ of \citet{pearl_causal_2016}
% definition is given:

\begin{quoting}
\textbf{Definition 3.3.1, The backdoor criterion}: Given an ordered pair of
variables (X, Y) in a directed acyclic graph G, a set of variables Z satisfies
the backdoor criterion relative to (X, Y) if no node in Z is a descendant of X,
and Z blocks every path between X and Y that contains an arrow into X.
\end{quoting}




\subsection{Software for this task?}
\label{sec:software-this-task}

Yes, there is software to do this. For example, DAGitty
(\Burl{http://www.dagitty.net/}) of which there is an R package, dagitty
(\Burl{https://cran.r-project.org/web/packages/dagitty/index.html}\footnote{This
  is the R package I am using to draw the figures in this document, in combination with the
  \texttt{drawdag} function of the
  ``rethinking'' package
  ---\Burl{https://github.com/rmcelreath/rethinking}}). But before using
software, I'd make sure to really understand the patterns, as shown in the
figures above.



\subsection{And d-separation?}
\label{sec:d-sep}

Some explanations of the backdoor criterion and the use of DAGs to find
dependencies and independencies make use of \textit{d-separation}.  But you can
explain and use the backdoor criterion without introducing more jargon, as we
have seen above (for example, \citealp{morgan_counterfactuals_2015} only use the
term d-separation in one footnote, though their procedure, which we have copied
above, actually implicitly uses the definition of d-separation). Anyway,
d-separation is well explained in Definition 2.4.1, p.\ 46 of
\citet{pearl_causal_2016} or in section ``Fine point 6.1'' of
\citet{hernan2020} and is very useful if you want to find all the
independencies and conditional independencies implied by a DAG.


% With what we have
% seen already, this will not be news:

% \begin{quoting}
%   Definition 2.4.1 (d-separation)
%   A path p is blocked by a set of nodes Z if and only if
%   \begin{itemize}
%   \item p contains a chain of nodes
% or a fork
%   \end{itemize}
% 1. p contains a chain of nodes
% or a fork
% the middle node B is in Z (i.e., B is conditioned on), or
% such that
% 2. p contains a collider
% such that the collision node B is not
% in Z, and no descendant of B is in Z.
% If Z blocks every path between two nodes X and Y, then X and Y are d-
% separated, conditional on Z, and thus are independent conditional on Z.
% \end{quoting}
%  Definition 2.4.1, p.\ 46 of \citet{pearl_causal_2016}


% Finally, a third way of understanding this. In section 7.2, pp.\ 85-86 of \citet{hernan2020}
%% Nope, just focuses on confounding.



% \section{Designed experiments and lack of confounding}\label{randomiz}
\section{Randomization and exchangeability in designed experiments}
In designed experiments with random assignment of experimental units (patients,
petri dishes, whatever) to treatments, there is no
confounding. There is no arrow to treatment assignment from anything else
precisely because treatment assignment is random. So go and redraw the very first
DAG, but remove the arrow into the treatment variable (Exercise).

Put differently, randomization leads to exchangeability: there is no association
between the potential outcomes and the actual treatment received.  The
relationship between randomization and exchangeability is discussed in
``Technical Point 2.1'', p.\ 15, in \citet{hernan2020}.  An intuitive explanation
(for a treatment with two possible values, ``treatment'' and ``control'') is the
following one in section 2.3.2, p.\ 9 of \cite{neal_causality_2020}:
``Exchangeability means that the treatment groups are exchangeable in the sense
that if they were swapped, the new treatment group would observe the same
outcomes as the old treatment group, and the new control group would observe the
same outcomes as the old control group. ''

We are ignoring possibly complicating issues in experimental studies, specially
with human subjects, such as partial compliance and whether to use ``intention to
treat'' or ``per-protocol'' analyses; see chapter 9 in \citet{hernan2020}. Note
that differential loss to follow up is a case of selection bias, not confounding;
see chapter 8 in \citet{hernan2020}. On both issues, see also chapter 5 in
\citet{westreich2019} for a shorter discussion.


\section{Terminology: exchangeability, ignorability}\label{ignorab}

More on ``exchangeability''. What follows is just for completeness, and because I
tend to trip over terminological issues.

As explained in pp.\ 459 and 460 of \cite{vanderweele2015}, the same condition is
often referred to by the following different names: ``exchangeability'',
``ignorability'', ``exogeneity'' or ``no-unmeasured-confounding''. For example,
\citet{morgan_counterfactuals_2015} in p.\ 53 (section 2.6) use ``ignorability''
for the same expression used to denote exchangeability in \citet{hernan2020}, and
\citet{pearl_causality_2009} in pp.79 and 341-342 also uses ``ignorability'' for
the same expression (more precisely, Pearl's expression is for conditional
exchangeability given covariates Z).  \citet{rosenbaum2017} defines ignorability
in note 33, p.\ 300, and p.\ 349, with the emphasis the other way around:
probability of treatment assignment independent of potential outcomes given
covariates. % But then,
  % \citet{Gelman2014} in exercise 8.10, p.\ 230, have an exercise where we are
  % asked to explain the differences --I think their usage of e
  % The reasons for receiving one treatment or another cannot be due to the outcome
  % itself nor to the treatment actually received.


\section{Randomization, exchangeability, counterfactuals, and potential
  outcomes}\label{counterf}

I have not used the words counterfactuals or potential outcomes. But
counterfactuals are (arguably) essential to understand why we can make causal
inferences from randomized experiments, and to understand what we are trying to
do when we try to eliminate confounding to try to do causal inference from
observational data. See further details in \citet{rosenbaum2017},
\citet{hernan2020}, \citet{morgan_counterfactuals_2015},
\citet{pearl2016} (and \citealp{woodward_making_2003} and \citealp[][ch.~5]{otsuka2023} for philosophical discussion). (\citealp{rosenbaum2017}, does not use DAGs at all; the others
do, and draw ---pun intended--- connections between counterfactuals and
DAGs).

Key message: even if you don't care about DAGs or making causal inferences
from observational data, counterfactuals are key for your inferences from
experimental data. In fact, you most likely think counterfactually (pun intended) a lot of the time: would you have had so much fun for the last hour or so had you not been reading these notes? \smiley{}


\section{Lord's paradox}

\citet{pearl2016} presents a very interesting analysis of what is called Lord's
paradox\footnote{This same paradox has been presented in many different places by
  other authors, and also by Pearl in other work; but the presentation in
  \citealp{pearl2016} I find much, much, clearer and insightful than the one in
  p.\ 85 of \citealp{pearl_causal_2016} or pp.\ 212-215 ---chapter 6--- of
  \citealp{pearl2018}.}. As Pearl explains, his paper ``address(es) the general
methodological issue of whether adjustments for preexisting conditions is
justified in group comparison applications''. A nice feature of this paper is
that Pearl presents both the original paradox as written by Lord as well as some
later modifications. Some of the versions differ because in the original one we
have a mediation problem, whereas in the second we have a confounding
problem. Even if the structure of the different presentations can seem
misleadingly similar, they are fundamentally different. In the mediation case,
whether or not to adjust for covariates depends on whether we want the direct
effect (this is what we would get if we adjust for the covariate) or the total
effect (what we get when we don't). In the confounding case, of course, we must
adjust for the covariate.



% {\small
%   \bibliography{covars-causal}
%   \bibliographystyle{jss2}
%   %% \bibliography{refs}
%   %% \bibliographystyle{myplainnat}
%   %% \bibliographystyle{mybibwithurl} %% not compatible with author-year
% }

\section{References}

(Note: some of the books below are ---legally and freely--- available from UAM's library and/or from the author's pages).

%% FIXME: in the future, use \bibliographystyle{jss2}
{\small
  \bibliography{refs-causal}
  \bibliographystyle{jss2}

  % \begin{thebibliography}{16}
  %   \providecommand{\natexlab}[1]{#1}
  %   \providecommand{\url}[1]{\texttt{#1}}
  %   \expandafter\ifx\csname urlstyle\endcsname\relax
  %     \providecommand{\doi}[1]{doi: #1}\else
  %     \providecommand{\doi}{doi: \begingroup \urlstyle{rm}\Url}\fi

  % \bibitem[Cole and Hern{\'a}n(2002)]{cole2002}
  %   Cole, S.~R. and Hern{\'a}n, M.~A.
  %   \newblock Fallibility in estimating direct effects.
  %   \newblock \emph{International Journal of Epidemiology}, 31\penalty0
  %   (1):\penalty0 163--165, February 2002.
  %   \newblock ISSN 0300-5771.
  %   \newblock \doi{10.1093/ije/31.1.163}.
  %   \newblock URL \url{https://doi.org/10.1093/ije/31.1.163}.

  % \bibitem[Hernan and Robins(2020)]{hernan2020}
  %   Hernan, M.~A. and Robins, J.~M.
  %   \newblock \emph{What If. {{Causal Inference}}}.
  %   \newblock {CRC Press}, 2020.
  %   \newblock ISBN 978-1-4200-7616-5.
  %   \newblock URL
  %   \url{https://www.hsph.harvard.edu/miguel-hernan/causal-inference-book/}.

  % \bibitem[{Hernandez-Diaz} et~al.(2006){Hernandez-Diaz}, Schisterman, and
  %   Hernan]{hernandez-diaz2006}
  %   {Hernandez-Diaz}, S., Schisterman, E.~F., and Hernan, M.~A.
  %   \newblock The {{Birth Weight}} "{{Paradox}}" {{Uncovered}}?
  %   \newblock \emph{American Journal of Epidemiology}, 164\penalty0 (11):\penalty0
  %   1115--1120, September 2006.
  %   \newblock ISSN 0002-9262, 1476-6256.
  %   \newblock \doi{10.1093/aje/kwj275}.
  %   \newblock URL
  %   \url{https://academic.oup.com/aje/article-lookup/doi/10.1093/aje/kwj275}.

  % \bibitem[{Hern{\'a}ndez-D{\'i}az} et~al.(2006){Hern{\'a}ndez-D{\'i}az},
  %   Schisterman, and Hern{\'a}n]{hernandez-diaz2006a}
  %   {Hern{\'a}ndez-D{\'i}az}, S., Schisterman, E.~F., and Hern{\'a}n, M.~A.
  %   \newblock Hern\'andez-{{D\'iaz}} et al. {{Respond}} to ``{{The Perils}} of
  %   {{Birth Weight}}''.
  %   \newblock \emph{American Journal of Epidemiology}, 164\penalty0 (11):\penalty0
  %   1124--1125, December 2006.
  %   \newblock ISSN 0002-9262.
  %   \newblock \doi{10.1093/aje/kwj277}.
  %   \newblock URL \url{https://doi.org/10.1093/aje/kwj277}.

  % \bibitem[Kline(2015)]{kline2015}
  %   Kline, R.~B.
  %   \newblock \emph{Principles and {{Practice}} of {{Structural Equation
  %   Modeling}}, {{Fourth Edition}}}.
  %   \newblock {The Guilford Press}, {New York}, 2015.
  %   \newblock ISBN 978-1-4625-2334-4.

  % \bibitem[McElreath(2020)]{rethinking_2020}
  %   McElreath, R.
  %   \newblock \emph{Statistical Rethinking: A {{Bayesian}} Course with Examples in
  %   {{R}} and {{Stan}}, 2nd Ed.}
  %   \newblock {CRC Press}, 2020.
  %   \newblock ISBN 978-0-367-13991-9.

  % \bibitem[Morgan and Winship(2015)]{morgan_counterfactuals_2015}
  %   Morgan, S.~L. and Winship, C.
  %   \newblock \emph{Counterfactuals and Causal Inference: Methods and Principles
  %   for Social Research, 2nd Ed}.
  %   \newblock {Cambridge University Press}, {New York, NY}, 2015.
  %   \newblock ISBN 978-1-107-58799-1 978-1-107-06507-9 978-1-107-69416-3.
  %   \newblock URL \url{http://dx.doi.org/10.1017/CBO9781107587991}.

  % \bibitem[Neal(2020)]{neal_causality_2020}
  %   Neal, B.
  %   \newblock \emph{Introduction to {{Causal Inference}}}.
  %   \newblock 2020.
  %   \newblock URL
  %   \url{https://www.bradyneal.com/Introduction_to_Causal_Inference-Dec17_2020-Neal.pdf}.


  % \bibitem[Otsuka(2023)]{otsuka2023}
  %   Otsuka, J.
  %   \newblock \emph{Thinking about Statistics: The Philosophical Foundations}.
  %   \newblock {Routledge}, {New York, NY}, 2023.
  %   \newblock ISBN 978-1-03-232610-8





% \bibitem[Pearl(2009)]{pearl_causality_2009}
% Pearl, J.
% \newblock \emph{Causality: Models, Reasoning, and Inference, 2nd Ed}.
% \newblock {Cambridge Univ. Press}, {New York, NY}, 2009.
% \newblock ISBN 978-0-521-89560-6.

% \bibitem[Pearl(2016)]{pearl2016}
% Pearl, J.
% \newblock Lord's {{Paradox Revisited}} \textendash{} ({{Oh Lord}}!
%   {{Kumbaya}}!).
% \newblock \emph{Journal of Causal Inference}, 4\penalty0 (2), 2016.
% \newblock ISSN 2193-3677.
% \newblock \doi{10.1515/jci-2016-0021}.
% \newblock URL
%   \url{https://www.degruyter.com/view/j/jci.2016.4.issue-2/jci-2016-0021/jci-2016-0021.xml}.

% \bibitem[Pearl and Mackenzie(2018)]{pearl2018}
% Pearl, J. and Mackenzie, D.
% \newblock \emph{The Book of Why: The New Science of Cause and Effect.}
% \newblock {Basic Books}, {New York, N.Y.}, 2018.

% \bibitem[Pearl et~al.(2016)Pearl, Glymour, and Jewell]{pearl_causal_2016}
% Pearl, J., Glymour, M., and Jewell, N.~P.
% \newblock \emph{Causal Inference in Statistics: A Primer}.
% \newblock {John Wiley \& Sons}, {Chichester, UK}, 2016.
% \newblock ISBN 978-1-119-18684-7.


% \bibitem[Peters et~al.(2017)Peters, Janzing, Scholkopf]{peters_causal_2017}
% Peters, J., Janzing, D., and Sch{\"o}lkopf, B.
% \newblock \emph{Elements of Causal Inference}.
% \newblock {MIT Press}
% \newblock ISBN 978-0-262-03731-0.
% \newblock URL
%   \url{https://library.oapen.org/bitstream/id/056a11be-ce3a-44b9-8987-a6c68fce8d9b/11283.pdf}



% \bibitem[Rosenbaum(2017)]{rosenbaum2017}
% Rosenbaum, P.
% \newblock \emph{Observation and {{Experiment}}: An {{Introduction}} to {{Causal
%   Inference}}}.
% \newblock {Harvard University Press}, {Cambridge, Massachusetts}, August 2017.
% \newblock ISBN 978-0-674-97557-6.

% \bibitem[Sober(2024)]{sober2024}
% Sober, E.
% \newblock Thoughts on {{Jun Otsuka}}'s {{Thinking}} about {{Statistics}} -- the {{Philosphical Foundations}}.
% \newblock \emph{Asian Journal of Philosophy}, 3\penalty0 (1), 2024.
% \newblock ISSN 2731-4642
% \newblock \doi{10.1007/s44204-024-00173-8}.
% \newblock URL

%  \url{https://link.springer.com/10.1007/s44204-024-00173-8}


% \bibitem[VanderWeele(2015)]{vanderweele2015}
% VanderWeele, T.
% \newblock \emph{Explanation in {{Causal Inference}}: Methods for {{Mediation}}
%   and {{Interaction}}}.
% \newblock {Oxford University Press}, {New York}, 2015.
% \newblock ISBN 978-0-19-932587-0.

% \bibitem[VanderWeele and Shpitser(2011)]{vanderweele2011}
% VanderWeele, T.~J. and Shpitser, I.
% \newblock A {{New Criterion}} for {{Confounder Selection}}.
% \newblock \emph{Biometrics}, 67\penalty0 (4):\penalty0 1406--1413, 2011.
% \newblock ISSN 1541-0420.
% \newblock \doi{10.1111/j.1541-0420.2011.01619.x}.
% \newblock URL
%   \url{https://onlinelibrary.wiley.com/doi/abs/10.1111/j.1541-0420.2011.01619.x}.

% \bibitem[Westreich(2019)]{westreich2019}
% Westreich, D.
% \newblock \emph{Epidemiology by {{Design}}: A {{Causal Approach}} to the
%   {{Health Sciences}}}.
% \newblock {Oxford University Press}, {New York, NY}, 2019.
% \newblock ISBN 978-0-19-066576-0.


% \bibitem[Woodward(2003)]{woodward2003}
% Woodward, J.
% \newblock \emph{Making Things Happen: A Theory of Causal Explanation}.
% \newblock {Oxford University Press}, {New York, NY}, 2003.
% \newblock ISBN 978-0-19-803533-6.

% \end{thebibliography}


% }



\end{document}















% In designed experiments with random assignment of experimental units (patients,
% petri dishes, whatever) to treatments, there is no
% confounding\footnote{Randomization leads to exchangeability: there is no
%   association between the potential outcomes and the actual treatment received.
%   The relationship between randomization and exchangeability is discussed in
%   ``Technical Point 2.1'', p.\ 15 in \citet{hernan2020}.  An intuitive
%   explanation (for a treatment with two possible values, ``treatment'' and
%   ``control'') is the following one in section 2.3.2, p.\ 9 of \cite{neal_causality_2020}:
%   ``Exchangeability means that the treatment groups are exchangeable in the sense
%   that if they were swapped, the new treatment group would observe the same
%   outcomes as the old treatment group, and the new control group would observe
%   the same outcomes as the old control group. ''

%   We are ignoring other issues, such as partial compliance
%   and whether to use ``intention to treat'' or ``per-protocol'' analyses; see
%   chapter 9 in \citet{hernan2020}. Note that differential loss to follow up is a
%   case of selection bias, not confounding; see chapter 8 in
%   \citet{hernan2020}. On both issues, see also chapter 5 in
%   \citet{westreich2019}.


%   More on ``exchangeability''. What follows is just for completeness, and because
%   I tend to trip over terminological issues.  As explained in pp.\ 459 and 460 of
%   \cite{vanderweele2015}, the same condition is often referred to by the
%   following different names: ``exchangeability'', ``ignorability'',
%   ``exogeneity'' or ``no-unmeasured-confounding''. For example,
%   \citet{morgan_counterfactuals_2015} in p.\ 53 (section 2.6) use
%   ``ignorability'' for the same expression used to denote exchangeability in
%   \citet{hernan2020}, and \citet{pearl_causality_2009} in pp.79 and 341-342
%   also uses ``ignorability'' for the same expression (more precisely, Pearl's
%   expression is for conditional exchangeability given covariates Z).
%   \citet{rosenbaum2017} defines ignorability in note 33, p.\ 300, and p.\ 349,
%   with the emphasis the other way around: probability of treatment assignment
%   independent of potential outcomes given covariates. % But then,
%   % \citet{Gelman2014} in exercise 8.10, p.\ 230, have an exercise where we are
%   % asked to explain the differences --I think their usage of e
%   % The reasons for receiving one treatment or another cannot be due to the outcome
%   % itself nor to the treatment actually received.
% }.

%% It would be great to clarify this terminological inconsistency.
%% Rosenbaum's definition is awesome, but is really about ignorability, which
%% I think is not exactly the same as exchangeability in Hernan and Robins.
% More formally, we would say there is exchangeability; see
% chapters 2 and 3 in \citet{hernan2020} and note 33, p.\ 300, in
% \citet{rosenbaum2017}.
%% Gelman et al also discuss this, but I think their use of exchangeability is different.