L1: Getting Started

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# L1: Getting Started
### Jean Morrison
### University of Michigan
### 2022-01-05 (updated: 2022-01-10)

---

`$\newcommand{\ci}{\perp\!\!\!\perp}$`

# Motivation

+ The idea that causality is interesting is easy to motivate.

+ The question "Why?" motivates nearly all scientific endeavors.

+ Causal inference formalizes what it means to answer this "Why?" question.

+ The idea that we need this formalization is much newer than the idea that causal questions are interesting.

---

# Example: Smoking and Lung Cancer

+ In 1900 only 140 cases of lung cancer were known in published medical literature.

+ By the 1920's incidence of lung cancer had increased dramatically.

+ Smoking was a hypothesized cause of lung cancer as early as 1912...

+ But so were:
  - Air pollution 
  - Asphalt dust from new roads
  - Poison gas from WWI
  - Influenza pandemic of 1918
  - Increasing use of radiography 
  - Increasing clinical awareness of lung cancer
  - Aging population

---

# The Case Against Smoking

- Observational studies showed a strong association between smoking and lung cancer.

+ Earliest studies used a case/control design. 
  + Followed by prospective studies matching healthy smokers and non-smokers by age, sex, and occupation and following them over time. 
  + All studies observed a large and robust association between smoking and lung cancer (Doll and Hill estimate an OR of 40 in 1954).

- Supporting evidence comes from animal studies in the 1930's and 1940's: Exposing animals to tobacco products causes cancer.

- Even more evidence from chemical analysis in the 1940's and 1950's: Cigarette smoke contains known cancer causing chemicals.
  + Much of this work is done by tobacco companies themselves.

- By the 1950's tobacco companies also believe that tobacco use causes cancer. This information is kept secret.

---

# Challenges to the Smoking-Lung Cancer Link

- Tobacco companies invested large amounts of money into research and advertising challenging the link between smoking and lung cancer.

- In the 1960's only one third of doctors believed smoking to be a major cause of lung cancer.

- RA Fisher was a famous challenger of the smoking `$\rightarrow$` lung cancer hypothesis:

+ Fisher pointed to a genetic factor linked to both smoking and lung cancer, arguing this factor may be a common cause of both. 
 + This concern about confounding is valid, but the effect size would need to be enormous.
 + The genetic hypothesis is also inconsistent with earlier low rates of lung cancer, animal studies, and reduced cancer rates in quitters.
 + It also disregards the possibility that smoking may be mediating the gene-cancer association.

---

# Why did Fisher (and others) Get it Wrong?

- Some have suggested that Fisher had conflicts of interest -- he had done work as a tobacco industry consultant and was himself a smoker.

- Fisher's statement that the association between smoking and lung cancer could be explained by a common cause is correct.

- But that model is inconsistent with many other lines of evidence.

---

# Lessons

- Causal inference cannot be achieved through only statistical procedures. It requires a model, assumptions, and information external to the study.

- All causal analyses of observational data require un-provable assumptions.

- Many interesting and important questions cannot be answered in a randomized trial.

+ We need theory and language that allows us to test causal hypotheses in observational data.

---

# Early Foundations of Causal Theory

- Neyman 1923: Notation and formalization of potential outcomes introduced.

- Fisher 1925: Physical randomization of units as the "reasoned basis" for inference.

- Wright 1921: Introduced graphical models and path analysis.

---

# Languages of Causality

+ Potential Outcomes/counterfactuals:
  - Proposes the existence of unobserved outcomes for each unit under different possible exposures or treatments.
  - First formalized by Neyman (1923), further developed by Donald Rubin (1974 and onward) and others.
  - "Rubin causal model".

--
+ Graphs:
  - Represents causal relationships between observed and unobserved variables as directed edges in a graph. 
  - Causal interventions are represented as modifications of the graph. 
  - Introduced by Wright (1921), further developed by Judea Pearl (1988 and onward) and others.

--
+ Structural Equations:
   - Represents causal relationships as a series of equations describing conditional probability distributions.
   - Also introduced by Wright in 1921.
   - More work by Pearl, Haavelmo, Duncan, and many more.

--
+ Under some conditions, all three languages are equivalent/mutually compatible.

---

# Counterfactuals/Potential Outcomes

+ What does it mean to say that `$A$` causes `$Y$`?

+ A counterfactual value, `$Y_i(A_i = a)$` is the value of `$Y$` the `$i$`th individual **would have had** if `$A$` had been **intervened on** and set to `$a$`.

+ Many equivalent notations:
  - `$Y(A = a)$`, `$Y(a)$`: I will primarily use these notations. 
  - `$Y^a$`: This is the main notation in Hernán and Robins.
  - `$Y\vert \ do(A = a)$`: This notation emphasizes the intervention of setting `$A$` equal to `$a$` and is favored by Judea Pearl. There are some subtle differences between the "do operator" and counterfactuals.

+ A counterfactual fundamentally supposes a hypothetical intervention (treatment).

---

# Example

For each person we observe:

+ If they wear a helmet when biking ( `$A_i = 1$` ) or not ( `$A_i = 0$` ).

+ If they sustain a head trauma in a given year ( `$Y_i = 1$` )  or not ( `$Y_i = 0$` ).

+ Below is the full table of counterfatual outcomes:

---
# Individual vs Average Treatment Effects

+ Sharp causal null: No effect of treatment for any individual, `$Y_i(A_i = 1) = Y_i(A_i = 0)$` for all `$i$`.

+ Average causal null: The average causal effect is zero, `$E[Y(A = 0)] = E[Y(A = 1)]$`.

+ In our example, the sharp null is false, but the average null is true.

# Measures of Treatment Effects

+ Average treatment effect (ATE): `$E[Y(1)] - E[Y(0)] = E[Y_i(A1) - Y_i(0)]$`

+ Risk ratio (RR): `$E[Y(0)]/E[Y(1)]$`

+ Odds ratio (OR; for binary outcomes): `$\frac{E[Y(1)]/(1-E[Y(1)])}{E[Y(0)]/(1-E[Y(0)]}$`

+ Null hypotheses ATE `$=0$`, RR `$=1$`, and OR `$=1$` are equivalent.

+ The ATE can be interpreted either as the difference in average outcome between groups or as the average difference.

+ This is not true for RR and OR -- RR is not equal to the average risk ratio over the population.

---

# Counterfactuals and Missing Data

+ The counterfactual framework turns causal inference into a missing data problem.

+ Even if we were able to observe `$A$` and `$Y$` for the entire population, uncertainty would remain in our estimate of the ATE because we cannot observe both `$Y_i(1)$` and `$Y_i(0)$` for the same individual.

+ This has been called the "fundamental problem of causal inference."

---

# Sample vs Population Treatment Effect

+ We very rarely sample the entire population of interest.

+ Sample average treatment effect (SATE): `$\frac{1}{n}\sum_{i = 1}^{n} Y_i(1) - \frac{1}{n}\sum_{i = 1}^{n} Y_i(0)$`

+ Population average treatment effect (PATE): `$E[Y(1)] - E[Y(0)]$`, with expectation is taken over a super-population.

+ Identifying the population is a scientific (rather than a statistical) task.

---

# Non-Deterministic Counterfactuals

+ So far we have seen two sources of uncertainty in the ATE: 
  
  - Missing counterfactual outcomes
  - Sampling variation
  
+ A third source is randomness in the counterfactual outcome.

+ Rather than thinking of `$Y_i(A_i = a)$` as a deterministic value, we can think of it as a random variable with individual specific (random) cdf `$F_{Y_i(a)}(y)$`.

+ We will abbreviate `$F_{Y_i(a)}(y)$` to `$F_{a,i}$`.

---

# Non-Deterministic Counterfactuals

+ If `$Y_i(A_i = a)$` is a random variable, the ATE is a double expectation:
 `$$E[Y(A = a)] = E\left \lbrace E[ Y_i(A_i = a) \vert F_{a,i} ] \right \rbrace$$`
with the inside expectation taken over the distribution of `$Y_i(A_i = a)$` and the outer expectation taken over the population.

+ Let `$F_{a} = E[F_{a,i}]$` be the average counterfactual cdf.

`$$E[Y(A =a)] = E\left[\int y \ dF_{a,i}(y) \right] = \int y \ dE[F_{a,i}(y)] = \int y \ dF_a(y)$$`
+ So, the average counterfactual value is the expectation w.r.t the average counterfactual cdf.

+ The distinction between deterministic and non-deterministic counterfactuals doesn't matter for average effects.

---

# Causation vs Association

![](img/1_fig1.png)

Fig 1.1 from HR

---

# Bike Helmet Example Continued

Average causal effect: `$E[Y(A = 1)] - E[Y(A = 0)] = 0.2 - 0.4 = -0.2$`

Observed association: `$E[Y \vert A = 1] - E[Y \vert A = 0] = 0.25 - 0.33 = -0.08$`

---
# Conditions for Identifying the Causal Effect

+ Suppose we only observe `$A$` and `$Y$`. When is it possible to estimate the ATE?

+ We must be able to estimate `$E[Y(a)]$` for all values of `$a$`. Therefore, we must have 
$$ E[Y(a)] = E[Y \vert A = a]$$

+ This is true under three assumptions:

- Consistency
  - Stable Unit Treatment Value Assumption (SUTVA)
  - Exchangeability (exogeneity)

---
# Consistency

+ The observed value of `$Y_i$` is the same as the counterfactual value of `$Y_i$` under the treatment `$a_i$`, where `$a_i$` is the treatment individual `$i$` actually recieved.

`$$Y_i = Y_i(A_i = a_i)$$`

Bike example:
+ A person's chances of head injury are the same if they wear a helmet of their own accord or if they are required to wear a helmet.

--
 
+ Whether or not consistency holds may depend on the nature of the hypothesized intervention.

---
# Stable Unit Treatment Value Assumption

1. There are no different versions of treatment available to an individual and the treatment level `$a$` is unambiguous for all values of `$a$`.

1. No interference: The counterfactual outcome for unit `$i$`, `$Y_i (A_i = a)$` is independent of the treatment received by other units in the study.

+ Formally, let `$\mathbf{A} = (A_1, \dots, A_n)$` be the vector of treatment assignments for all units with `$\mathbf{a}$` being a single realization of `$\mathbf{A}$`. Let `$a_i$` be the `$i$`th element of `$\mathbf{a}$` and `$\mathcal{A}^n$` be the sample space of `$\mathbf{A}$`. Let `$Y_i(\mathbf{A} = \mathbf{a})$` be the counterfactual value of `$Y_i$` under the treatment vector `$\mathbf{a}$`. No interference is the condition that

$$
Y_i(\mathbf{A}= \mathbf{a}) = Y_i(A_i = a_i) \ \  \ \forall\ \ \mathbf{a} \in \mathcal{A}^{n}
$$

Pair discussion:

+ What do these assumptions look like in the bike helmet example?

+ Can you think of a time "No interference" may not hold?

---

# Exchangeability

+ Exchangeability: `$Y(a) \ci A$`.

+ Question: How is `$Y(a) \ci A$` different from `$Y \ci A$`?

+ Mean exchangeability: `$E[Y(a) \vert A = a^\prime] = E[Y(a) \vert A = a^{\prime \prime}]$` for all pairs `$a^\prime, a^{\prime \prime} \in \mathcal{A}.$`

+ Mean exchangeability is sufficient to prove `$E[Y(a)] = E[Y \vert A = a].$`

+ For dichotomous `$Y$`, mean exchangeability and exchangeability are equivalent.

+ What about for non-dichotomous `$Y$`?

+ Full exchangeability: Let `$Y^{\mathcal{A}} = \left \lbrace Y(a), Y(a^\prime), \dots \right \rbrace$` be the set of all counterfactual outcomes ( `$Y^{\mathcal{A}} = \left \lbrace Y(1), Y(0) \right \rbrace$` for a dichotomous treatment). Full exchangeability states that

$$
Y^{\mathcal{A}} \ci A 
$$

---

# Exchangeability in the Bike Helmet Example:

`$E[Y(A = 0) \vert A = 0] = 0.33$`,   `$E[Y(A = 0) \vert A = 1] = 0.5$`

`$E[Y(A = 1) \vert A = 0] = 0.17$`,   `$E[Y(A = 1) \vert A = 1] = 0.25$`

---

# Identification Theorem

Theorem: If consistency, SUTVA, and exchangeability hold, then `$$Y(a) \overset{d}{=} Y | A = a,$$` where `$\overset{d}{=}$` means equal in distribution.

Proof:

`$$P[Y(a) \leq y] = P[Y(a) \leq y \vert A = a] \ \ \ \text{(exchangeability)}$$`
`$$= P[Y \leq y \vert A = a] \ \ \  \text{(consistency)}$$`
--

Corrolary: If consistency, SUTVA, and exchangeability hold then `$E[Y(a)] = E[Y \vert A = a]$`

---

# Where did SUTVA come in?

+ If the levels of `$A$` are not clearly defined, the causal question is ill-defined (i.e. `$Y(a)$` is poorly defined).

+ In the presence of interference, there is no single value of `$Y_i(a_i)$`. Instead, we must discuss `$Y_i(\mathbf{a})$`, the potential outcome given the entire vector of treatment assignments.

---

# Simple Randomized Experiments

+ Units are assigned a treatment value using a randomization procedure that is independent of all unit characteristics (e.g. flip a coin).

+ For now, we assume full compliance (everyone assigned treatment `$a$` receives treatment `$a$`).

+ Exchangeability holds by design.

+ So, we can estimate the ATE as long as consistency and SUTVA hold.

+ One estimator is just the difference in average outcomes (more on estimators in HW1):
`$$\frac{1}{n_{1}}\sum_{i: A_i = 1}Y_i - \frac{1}{n_2}\sum_{i:A_i = 0}Y_i = \bar{Y}_1 - \bar{Y}_0$$`

---

# Conditionally Randomized Experiments

+ Units are assigned a treatment with probability depending on a set of features, `$L$`.

+ If `$L$` and `$Y(a)$` are not independent, then exchangeability does not (generally) hold.

+ However, we can still identify the ATE if we have access to the randomization features `$L$`.

---

# Example

+ We are doing an experiment of a new treatment for a disease. Some patients will receive the new treatment ( `$A = 1$` ), 
while the rest will receive standard of care ( `$A = 0$` ).

+ Let `$L = 0$` indicate that a patient is less sick and `$L = 1$` indicate that they are more sick.

+ We decide on a randomization scheme in which sicker patients are more likely to receive the new treatment. We set `$P(A = 1 \vert L = 0) = 0.5$` and `$P(A = 1 \vert L = 1) = 0.75$`.

+ We observe if each patient dies before a set time point ( `$Y = 1$` for death, `$Y = 0$` for survival).

---

# Conditional Exchangeability

+ Notice that our trial looks like two fully randomized trials combined. 
  
    - In one trial, the target population is patients with `$L = 0$` and the treatment probability is 0.5.
    - In the other, the target population is patients with `$L = 1$` and the treatment probability is 0.75.

+ Conditional exchangeability captures the idea that data are randomized *within* levels of `$L$`.

+ Conditional exchangeability holds with respect to a set of variables `$L$`, if

`$$Y(a) \ci A\ \vert\ L$$`
---
# Stratum Specific Causal Effects and Standardization

+ Exchangeability holds within levels of `$L$`, so `$E[Y(a) \vert L = l]$` is identifiable.

`$$E[Y(a) \vert L = l] = E[Y \vert A = a, L = l]$$`

+ If we want to estimate the population level marginal counterfactual value of `$Y$` under treatment `$A = a$`, we can simply weight our estimates
by the population frequency of `$L$`:
$$
E[Y(a)] = \sum_{l}E[Y(a) \vert L = l]P[L = l]
$$
--

+ This is called the standardized mean (standardized by whatevery population frequencies of `$L$` you choose).

---

# Positivity

+ Of course, the standardization trick doesn't work if, within one level of `$L$`, patients never (or always) receive treatment.

+ The positivity condition states that at all individuals have some chance of receiving any treatment:

`$$P[A = a \vert L = l] > 0 \ \ \forall a, l$$`

---

# Identification Theorem (Conditional)

Theorem: If consistency, SUTVA, conditional exchangeability, *and positivity* hold, then `$$Y(a) \vert\ L =l \overset{d}{=} Y |\ L = l, A = a.$$`

We can use exactly the same proof as the non-conditional theorem, conditioning on `$L$` in each step.

Proof:

`$$P[Y(a) \leq y \vert L = l] = P[Y(a) \leq y \vert L=l, A = a] \ \ \ \text{(conditional exchangeability)}$$`
`$$= P[Y \leq y \vert L=l, A = a] \ \ \  \text{(consistency)}$$`

---

# Inverse Probability Weighting

+ Rather than using the standardization method, we can think of our trial as a weighted sampling from a larger, fully randomized trial with `$2N$` participants.

+ This *pseudo-population* contains two members for every member in our trial, one receiving each treatment.

+ In the pseudo-population, `$Y(a) \ci A$` so the conditional mean, `$E[Y \vert A = a]$` estimates the counterfactual mean `$E[Y(a)]$`.

---

# Inverse Probability Weighting

+ We can imagine that each individual in our trial was sampled from the larger population with probability conditional on `$L$` and `$A$`.
 
 - In our study we selected half of participants with `$A_i = 0$` and `$L_i = 0$`
 - Half of participants with `$A_i = 1$` and `$L = 0$`
 - One quarter of participants with `$A_i = 0$` and `$L = 1$` 
 - Three quarters of participants with `$A_i = 1$` and `$L = 1$`

+ We can recover the estimate from the pseudo-population by weighting each participant by the number of units in the larger study that they represent:
  
  - `$A_i=0$`, `$L_i=0$`: `$1/0.5 = 2$`
  - `$A_i = 1$`, `$L_i = 0$`: `$1/0.5 = 2$`
  - `$A_i = 0$`, `$L_i = 1$`: `$1/0.25 = 4$`
  - `$A_i = 1$`, `$L_i = 0$`: `$1/0.75 = 1.33$`

---

# Inverse Probability Weighting

+ Formally, let `$f_{A \vert L}(a\vert l)$` be the conditional pdf of `$A$` given `$L$`.

+ We assume that `$f_{A \vert L}(a\vert l) > 0$` for all `$a$` and `$l$` s.t `$P[L = l] > 0$`.

+ The IP weighting for individual `$i$` is `$W^A_i = 1/f_{A\vert L}(a_i \vert l_i)$`.

+ The IP weighted mean for treatment level `$a$` is `$E\left[\frac{I(A=a)Y}{f(A\vert L)}\right]$`

---

# Equivalence of IP Weighting and Standardization

+ We will assume that `$A$` and `$L$` are discrete and `$f(a \vert l) = P[A = a \vert L = l] > 0$` for all `$l$` with `$P[L = l] > 0$`.

+ Use the iterated expectation formula:

`$$E\left[\frac{I(A=a)Y}{f(A\vert L)}\right] = E_L \left \lbrace E_{A} \left\lbrace E_{Y}\left[\frac{I(A=a)Y}{f(A\vert L)} \vert A, L \right]\right\rbrace \right\rbrace$$`
`$$=\sum_l \frac{E[Y\vert A = a, L = l]}{f(a\vert l)} f(a \vert l) P[L = l]$$`
`$$= \sum_l E[Y\vert A = a, L = l] P[L = l]$$`

+ This proof extends to continuous `$L$` but not to continuous `$A$`.

+ If conditional exchangeability holds, then both the IP weighted mean and the standardized mean estimate `$Y(a)$`.

---

# Causal Effects from in an Observational Data

+ None of our four identification conditions consistency, SUTVA, conditional exchangeability, and positivity require that our data is from a randomized trial.

+ However, these are much stronger assumptions in observational data. 
---

# Consistencey
  
- Consistency says: The outcome we observed for unit `$i$` ( `$Y_i$` ), who received treatment `$a$` is the same as the outcome we *would have observed* if we had intervened and set `$A_i$` to `$a$`.

`$$A_i = a \Rightarrow Y_i = Y_i(a)$$`

- In a trial with an intervention, consistency is almost tautological. 
    
    + We *did* intervene and set `$A_i$` to `$a$`.

- In an observational study we should think about if consistency is justified.

+ People may change their behavior if they receive an intervention vs. choosing a behavior independently.
  
---
# Conditional Exchangeability

+ In a trial, exchangeability is guaranteed by the study design. 
  - The researchers control the assignment mechanism and therefore know all of the features which contribute to treatment probabilities.
  
+ In observational studies, treatment assignment occurs "naturally".
  - Identifying a set of variables to give conditional exchangeability requires assumptions and external information.
  - It may not be possible to measure all necessary variables.

---

# Positivity

+ In a trial, positivity is guaranteed by design.

+ In observational data, even if we know a set `$L$` of variables such that `$Y(a) \ci A\ \vert \ L$`, there may be levels `$L$` for which `$P(A = a \vert L = l)$` is close to or exactly zero.

---

# The Target Trial

- Hernán and Robins argue that in order to identify a causal effect in observational data, we must have in mind a target trial that would identify the same parameter if it were feasible.

- This includes clearly and specifically defining a hypothetical intervention.

- This is often tricky (but not necessarily impossible): Consider the statements
  
  + "Earning a college degree will increase your earnings."
  + "He was pulled over because he is Black."
  + "Obesity causes heart disease".