Part III of this book discusses causal inference with observational studies under two assumptions: unconfoundedness and overlap. Both are strong assumptions and are likely to be violated in practice. This chapter will discuss the difficulties of the unconfoundedness assumption. Chapters 17–19 will discuss various strategies for sensitivity analysis in observational studies with unmeasured confounding. Chapter 20 will discuss the difficulties of the overlap assumption.
Pearl, (1995) introduced the causal diagram as a powerful tool for causal inference in empirical research. Pearl, (2000) is a textbook on the causal diagram. Here I introduce the causal diagram as an intuitive tool for illustrating the causal relationships among variables.
For example, if we have the causal diagram
and focus on the causal effect of
on
,
we can read it as the following data-generating process:
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where
for both
.
In the above, covariates
are generated from a distribution
, the treatment assignment is a function of
with a random error term
, and the potential outcome
is a function of
,
and a random error term
. We can easily read from the equations that
, i.e., the unconfoundedness assumption holds.
If we have a causal diagram
we can read it as the following data-generating process:
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where
for both
. We can easily read from the equations that
but
, i.e., the unconfoundedness assumption holds conditional on
but does not hold conditional on
only. In this case,
is an unmeasured confounder. In this diagram,
is called an unmeasured confounder.
The unconfoundedness assumption
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implies that
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So the unconfoundedness assumption basically requires that the counterfactual distribution
equals the observed distribution
, and the counterfactual distribution
equals the observed distribution
. Because the counterfactual distributions are not directly identifiable from the data, the unconfoundedness assumption is fundamentally untestable without additional assumptions. I will discuss two strategies to assess the unconfoundedness assumption. Here, “assess” is a weaker notion than “test”. The former is referred to as supplementary analysis that supports or undermines the initial analysis, but the latter is referred to as formal statistical testing.
Assume that
is an outcome similar to
and ideally, shares the same confounding structure as
. If we believe
, then we also tend to believe
.
Moreover, we know, a priori, the effect of
on
:
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An important example is that
. A causal diagram satisfying these requirements is below:
Cornfield et al., (1959) studied the causal role of cigarette smoking on lung cancer based on observational studies. They controlled for many important background variables but it is still possible to have some unmeasured confounders biasing the observed effects. To strengthen the evidence for causation, they also reported the effect of cigarette smoking on car accidents, which was close to zero, the anticipated effect based on biology. So even if they could not rule out unmeasured confounding in the analysis, this supplementary analysis based on a negative outcome makes the evidence of the causal effect of cigarette smoking on lung cancer stronger.
Imbens and Rubin, (2015) suggested using the lagged outcome as a negative outcome. In most cases, it is reasonable to believe that the lagged outcome and the outcome have a similar confounding structure. Since the lagged outcome happens before the treatment, the average causal effect on it must be
. However, their suggestion should be used with caution since in most studies we simply treat lagged outcomes as an observed confounder.
In some sense, the covariate balance check in Chapter 11 is a special case of using negative controls. Similar to the problem of using lagged outcomes as negative controls, those covariates are usually a part of the unconfoundedness assumption. Therefore, the failure of the covariate balance check does not really falsify the unconfoundedness assumption but rather the model specification of the propensity score.
Observational studies of elderly persons have shown that vaccination against influenza remarkably reduces one’s risk of pneumonia/influenza hospitalization and all-cause mortality in the following season, after adjustment for measured covariates. Jackson et al., (2006) were skeptical about the large magnitude and thus conducted supplementary analysis on negative outcomes. Vaccination often begins in the fall, but influenza transmission is often minimal until the winter. Based on biology, the effect of vaccination should be most prominent during influenza season. But Jackson et al., (2006) found a greater effect before the influenza season, suggesting that the observed effect is due to unmeasured confounding.
Jackson et al., (2006) seems the most convincing one since the influenza-related outcomes before and during the influenza season should have similar confounding patterns. Cornfield et al., (1959)’s additional evidence seems weaker since car accidents and lung cancer have very different causal mechanisms with respect to cigarette smoking. In fact, Fisher, (1957)’s critique was that the relationship between cigarette smoking on lung cancer may be due to an unobserved genetic factor (see Chapter 17). Such a genetic factor might affect cigarette smoking and lung cancer simultaneously, but it seems unlikely that it also affects car accidents.
Lipsitch et al., (2010) is a recent article on negative outcomes. Rosenbaum, (1989) discussed the role of known effects in causal inference.
Negative exposures are duals of negative outcomes.
Assume
is a treatment variable similar to
and shares the same confounding structure as
. If we believe
, then we tend to believe
Moreover, we know, a priori, the effect of
on 
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An important example is that
A causal diagram satisfying these requirements is below:
Sanderson et al., (2017) give many examples of negative exposures in determining the effect of intrauterine exposure on later outcomes by comparing the association of maternal exposure during pregnancy with the outcome of interest, with the association of paternal exposure with the same outcome. They review studies on the effect of maternal and paternal smoking on offspring outcomes, and studies on the effect of maternal and paternal BMI on later offspring BMI and autism spectrum disorder. In these examples, we expect the association of maternal exposure with the outcome to be larger than that of paternal exposure with the outcome.
The unconfoundedness assumption is fundamentally untestable without additional assumptions. Although negative outcomes and negative controls in observational studies cannot prove or disprove unconfoundedness, using them in supplementary analyses can strengthen the evidence for causation. However, it is often non-trivial to conduct this type of supplementary analysis because it involves more data and more importantly, a deeper understanding of the causal problems to find convincing negative outcomes and negative controls.
We have discussed many methods for estimating causal effects under the unconfoundedness assumption:
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This is an assumption conditioning on
. It is crucial to select the right set of
that ensures the conditional independence.
Rosenbaum, 2002b () wrote that “there is no reason to avoid adjustment for a variable describing subjects before treatment.” Similarly, Rubin, (2007) wrote that “typically, the more conditional an assumption, the more acceptable it is.” Both argued that we should control for all observed pretreatment covariates. VanderWeele and Shpitser, (2011) called it the pretreatment criterion.
Pearl disagreed with this recommendation and gave two counterexamples below.
M-bias appears in the following causal diagram with an M-structure:
We can read from the diagram the data-generating process:
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where
are independent random error terms. In the above causal diagram,
is observed, but
and
are unobserved.
If we change the value of
, the value of
will not change at all. So the true causal effect of
on
must be
. From the data-generating equations, we can read that
, so the association between
and
is
, and, in particular,
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This means that without adjusting for the covariate
, the simple estimator is unbiased for the true parameter.
However, if we condition on
, then
, and consequently,
and
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in general. To gain intuition, we consider the case with Normal linear models37:
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where
.
We have
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but by the result in Problem 1.3, the partial correlation coefficient between
and
given
is38
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the product of the coefficients on the path from
to
.
So the unadjusted estimator is unbiased but the adjusted estimator has a bias proportional to
.
The following simple example illustrates M-bias.
Consider the following causal diagram:
with the data generating process39
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where
are IID
. In this data-generating process, we have
, and
affects
only through
.
The unadjusted estimator is
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which has bias
. The adjusted estimator from the OLS of
on
satisfies
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Solve the above linear system of
to obtain the formula of
:
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(81) |
which has bias
. I relegate the details for solving the linear system of
as Problem 16.1.
So the unadjusted estimator has a smaller bias than the adjusted estimator. More interestingly, the stronger the association between
and
is (measured by
), the larger the bias of the adjusted estimator is.
The mathematical derivation is not extremely hard. But this type of bias seems rather mysterious. Here is the intuition. The treatment is a function of
,
, and other random errors. If we condition on
, it is merely a function of
and other random errors. Therefore, conditioning on
makes
less random, and more critically, makes the unmeasured confounder
play a more important role in
. Consequently, the confounding bias due to
is amplified by conditioning on
. This idealized example illustrates the danger of over-adjusting for some covariates.
Heckman and Navarro-Lozano, (2004) observed this phenomenon in simulation studies.
Wooldridge, (2016, technical report in 2006) verified it in linear models.
Pearl, 2010a (); Pearl, (2011) explained it using causal diagrams.
Ding et al., 2017b () provided a more general theory as well as some intuition for this phenomenon.
This type of bias is called Z-bias because, in Pearl’s original papers, he used the symbol
for our variable
. Throughout the book, however,
is used for the treatment variable. In Part V of this book, we will call
an instrumental variable if it satisfies the causal diagram presented in this subsection. This justifies the instrumental variable bias as another name for this type of bias.
The following simple example illustrates Z-bias.
We never know the true underlying data-generating process which can be quite complicated. However, the following causal diagram helps to clarify many ideas. It already rules out the possibility of
-bias discussed in Section 84.1.
The covariates above have different features:
affects both the treatment and the outcome. Conditioning on
ensures the unconfoundedness assumption, so we should control for
.
is pure random noise not affecting either the treatment or the outcome. Including it in the analysis does not bias the estimate but introduces unnecessary variability in finite samples.
is an instrumental variable that affects the outcome only through the treatment. In the diagram above, including it in the analysis does not bias the estimate but increases the variability of the estimate. However, with unmeasured confounding, including it in the analysis amplifies the bias as shown in Section 84.1.
affects the outcome only but not the treatment. Without conditioning on it, the unconfoundedness assumption still holds. Since they are predictive of the outcome, including them in analysis often improves precision.
is affected by the treatment and outcome. It is a post-treatment variable, not a pretreatment covariate. We should not include it if the goal is to infer the effect of the treatment on the outcome. We will discuss issues with post-treatment variables in causal inference in Part VI of this book.
If we believe the above causal diagram, we should adjust for at least
to remove bias and more ideally, further adjust for
to reduce variance.
Verify (81).
Sir David Cox calls the following result Cochran’s formula (Cochran,, 1938; Cox,, 2007) and econometricians call it the omitted variable bias formula (Angrist and Pischke,, 2008). A special case appeared in Fisher, (1925). It is also a counterpart of the Frisch–Waugh–Lovell theorem in Chapter 31.C.
The formula has two versions. All vectors below are column vectors.
[(1)]
(Population version) Assume
are IID, where
is a scalar,
has dimension
, and
has dimension
.
We have the following OLS decompositions of random variables
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(82) | ||
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(83) | ||
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(84) |
Equation (82) is called the long regression, and Equation (83) is called the short regression. In Equation (84),
is a matrix because it is a regression of a vector on a vector. You can view (84) as regression of each component of
on
.
Show that 
(Sample version) We have an
vector
, an
matrix
, and an
matrix
. We do not assume any randomness. All results below are purely linear algebra.
We can obtain the following OLS fits:
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where
are the residuals.
Again, the last OLS fit means the OLS fit of each column of
on
, and therefore the residual
is an
matrix.
Show that
.
Remark: The product terms
and
are often referred to as the omitted-variable bias at the population level and sample level, respectively.
Imbens, (2020) reviews and compares the roles of potential outcomes and causal diagrams for causal inference.
37. It is not ideal for our discussion of binary
, but it simplifies the derivations. Ding and Miratrix, (2015) gave a detailed discussion with more natural models for binary
.
38. The notation
reads as “proportional to” and allows us to drop some unimportant constants.
39. Again, we generate continuous
from a linear model to simplify the derivations. Ding et al., 2017b () extended the theory to more general causal models, especially for binary
.
本书:A First Course in Causal Inference,作者 Peng Ding。原文:arXiv:2305.18793v2,按 CC BY 4.0 许可发布。本站(yuanens.com)把 arXiv 网页版改成分章的纯 HTML,把公式渲染成图片,方便在 Kindle 等电子书阅读器上看,内容没有改动。转换难免有错,以原文为准。本站与作者和出版社无关。