# Instrumental Variables Alex Cardazzi All materials can be found at alexcardazzi.github.io. ## A New Approach So far, we’ve discussed randomized control trials, differences-in-differences, and synthetic control, as well as the idea of controlling for observable characteristics. RCTs are the gold standard of causal inference due to their ensuring random treatment assignment. DiD uses changes in a control group to estimate how the treatment group would have changed in the absence of treatment. Controlling for observable characteristics tries to balance the two samples so that treatment appears to be randomly assigned between groups. Synthetic control, as previously mentioned, tries to split the difference between this idea and DiD by building a weighted synthetic comparison unit to estimate counterfactual changes. While these methods are all theoretically different, they are very similar in spirit. The next method we’ll introduce is called **Instrumental Variables** (or IV for short), and it addresses the identification problem in a way that is different altogether. The idea behind IV is to find something that randomly, even if only partially, determines treatment status. Then, we can use this variable (called an *instrument*) to predict treatment status. By predicting (or *instrumenting for*) treatment using this variable, we are effectively eliminating the variation from all the other “stuff” in our setting. Admittedly, this will probably be the most difficult causal inference approach to wrap your head around, so let’s dive into an example. ## Military Experience Let’s ask a simple, albeit big, question: **how does military experience effect civilian earnings?** Suppose we have individual-level data containing information about one’s military experience and their earnings. This question was famously addressed by Joshua Angrist in his 1990 article [“Lifetime Earnings and the Vietnam Era Draft Lottery: Evidence from Social Security Administrative Records”](https://www.jstor.org/stable/2006669) Before addressing IV, let’s think backwards through the causal inference approaches we’ve already learned. Right off the bat, we can write off synthetic control since this isn’t a case study. Second, let’s think about comparing people who look alike on paper. We can certainly find two individuals from the same high school, who got the same grades, were exposed to the same environments, but one opted for the military and one did not. Would these two individuals be good counterfactuals for one another? In terms of observable characteristics, yes! However, could there be something unobservable that is driving the decision to enlist while also causing future earnings? Almost definitely. Individuals who join the military, even when observationally similar to others, often have very different personalities/circumstances than civilians. For example, maybe these people are more aggressive and/or have a more intense work ethic. These characteristics are almost never observable let alone measureable/quantifiable. So, if we only compare people who look alike on paper, we’d probably be unable to account for personality/circumstances/etc., making this approach unsuitable. Next, we have difference-in-differences. If we’ve already convinced ourselves that personality is a confounder we can’t control for, we can probably rule out parallel trends as well. At this point, you might feel a little stuck or like this question is unanswerable. Let’s think about what the DAG for this setting would look like. In reality, this is a very complicated relationship, but what we’re really concerned about is some backdoor, such as personality, between military experience and civilian earnings. Drawing a simple DAG for this would look like the following:

Code

``` r library("dagitty") dag <- dagitty("dag { Military [exposure] Earnings [outcome] Military -> Earnings Military <- Personality -> Earnings }") plot(dag) ```

Plot

If we could control for personality, we wouldn’t have a problem. Without being able to observe/quantify it, though, we don’t have many options. The only way to identify the causal effect would be through randomization. Ethically/legally, can we implement an RCT to randomly assign people to military service? Well… kind of. Military drafts generate random variation in the probability that someone serves in the military. This is not *really* an RCT, though. First off, the military only drafts people of certain observable characteristics. This is not really a problem for us since we can control for this by subsetting our sample so we are only looking at potential draftees. Second, and more importantly, the draft does not perfectly determine who serves and who doesn’t. In this setting, there are four “types” of people: 1. **Compliers**: Individuals whose choice will be determined by their draft status. If they’re drafted, they’ll serve. If they’re not drafted, they’ll remain a civilian. 2. **Always Takers**: Individuals who enlist in the military regardless of whether they get drafted (e.g. people who want to be in the military). 3. **Never Takers**: Individuals who never enlist regardless of whether they get drafted (e.g. conscientious objectors). 4. **Defiers**: Individuals who refuse to serve if drafted, but enlist if not drafted. These people are the opposite of compliers.

Of course, these types of people/units exist in all settings, but it’s especially important to discuss them when talking about IV. We’ll revisit this later in the module.

Hopefully, it’s clear that the draft introduces some element of randomization. However, given these different groups, it may not be as clear how to use it for identifying the causal link between military service and civilian earnings. This is where instrumental variables come in. Let’s redraw the dag to identify the paths in this setting, but also include draft status as a factor.

Code

``` r dag <- dagitty("dag { Military [exposure] Earnings [outcome] Draft -> Military -> Earnings Military <- Personality -> Earnings }") plot(dag) paths(dag) ```

Output

$paths [1] "Military -> Earnings" "Military <- Personality -> Earnings" $open [1] TRUE TRUE

Plot

Of course, adding this factor onto the end of the DAG does not modify the already existing paths. However, we can use the `instrumentalVariables()` function to give us a list of possible instruments. ``` r instrumentalVariables(dag) ```

Output

Draft

We are going to predict, or *instrument*, military enlistment using draft status, which creates a nifty loophole for us. There are two ways of thinking about this. First, by using the draft to predict military enlistment, we force the treatment to only vary when draft status varies. This will shut down the influence personality has on military enlistment. On the other hand, you can think of this as shifting treatment from military to draft. Initially, we had the backdoor path $\text{Military} \leftarrow \text{Personality} \rightarrow \text{Earnings}$. However, by shifting the treatment to $\text{Draft}$, we create a collider along this path: $\text{Draft} \rightarrow \text{Military} \leftarrow \text{Personality} \rightarrow \text{Earnings}$. To interpret our estimate as the causal effect of military on earnings, we need to make sure there’s no other paths from our instrument (draft) to our outcome (earnings). Let’s suppose there were two other factors, “something” and “else”, that both caused earnings. Further, suppose “something” also causes draft status but “else” is caused by draft status. What would this DAG look like?

Code

``` r dag <- dagitty("dag { Military [exposure] Earnings [outcome] Draft -> Military -> Earnings Military <- Personality -> Earnings Draft <- Something -> Earnings Draft -> Else -> Earnings }") plot(dag) paths(dag) ```

Output

$paths [1] "Military -> Earnings" [2] "Military <- Draft -> Else -> Earnings" [3] "Military <- Draft <- Something -> Earnings" [4] "Military <- Personality -> Earnings" $open [1] TRUE TRUE TRUE TRUE

Plot

What does `dagitty` suggest for us now when we ask for instruments? ``` r instrumentalVariables(dag) ```

Output

Draft | Else, Something

It still tells us that draft is a candidate for an instrument, but it also requires us to control for “something” and “else” as well. To see why this is, let’s keep thinking about this as switching our treatment from military to draft. The paths in this case would look like the following:

Code

``` r dag <- dagitty("dag { Draft [exposure] Earnings [outcome] Draft -> Military -> Earnings Military <- Personality -> Earnings Draft <- Something -> Earnings Draft -> Else -> Earnings }") as.data.frame(paths(dag)) ```

Output

paths open 1 Draft -> Else -> Earnings TRUE 2 Draft -> Military -> Earnings TRUE 3 Draft -> Military <- Personality -> Earnings FALSE 4 Draft <- Something -> Earnings TRUE

Right off the bat, the last path should set off some alarms. This is an open backdoor path, so we definitely need to control for “something” to close it. The third path is already closed because it’s a collider, so we don’t want to touch this path. With two paths left, we need to think carefully about whether we need to control for anything more. The second path is the effect of draft status on earnings, through military enlistment. This is the path we care about, so we want to keep this path open. Finally, we’re left with the first path. If we leave this path open, we would estimate the *total* effect of draft status on earnings. This would be some combination of “else” and military enlistment. Of course, we’re not interested in “else”, so by controlling for it, we’re allowing draft to effect earnings but *only* through the influence of military enlistment. Essentially, we’re purging military enlistment of all the “bad” variation we weren’t interested in. ## IV Math What does instrumental variable estimation look like? The process is fairly simple in words, but there are a few steps. 1. Select a candidate instrument. 2. Model the treatment using the instrument. This is called the **first stage**. 3. Check if the instrument does a “good job” explaining treatment. 4. Use the model to generate predicted treatment values. 5. Model the outcome using the predicted treatment values. This is called the **second stage**. This two-step procedure is called **two-stage least squares** (or 2SLS). For a section labeled “math”, these steps probably seem pretty wordy and vague. They’re supposed to. Linear regression is just one way of fitting models and generating predictions. You can use other methods like neural networks, random forests, etc., but these methods are outside the scope of this course. Still, you should be aware that even though I am going to use OLS, and most economists will use OLS, there are other methods of estimation. So, what does the regression look like? Typically, you’ll see four models when people present IV estimates. First, people present the endogenous regression results for a baseline. Next, you might see what people call “reduced form” equations, where the instrumental variable is substituted into the endogenous equation for the endogenous treatment variable. Finally, you’ll have the first stage and the second stage regression equations. Below, I have put each of these regressions in a table where $Y$ represents the outcome, $D$ represents the treatment, $Z$ represents the instrument, and $X$ represents control variables. | Type | Equation | |----|:--:| | Naïve / Endogenous | $Y_i = \alpha_1 + \beta D_i + \omega_1 X_i + e_i$ | | Reduced Form | $Y_i = \alpha_2 + \gamma Z_i + \omega_2 X_i + e_i$ | | First-Stage | $D_i = \alpha_3 + \rho Z_i + \omega_3 X_i + e_i$ | | Second-Stage | $Y_i = \alpha_4 + \delta \widehat{D_i} + \omega_4 X_i + e_i$ | Types of Equations We won’t focus too much on the first equation, since we know that this will produce biased coefficient estimates. Rather, we’ll discuss the next three. The second equation in this table is the reduced form equation. This quantifies the effect of the instrument on the outcome. If the only open path from instrument to outcome is through the treatment, then this, in a way, can be thought of as causal. So what’s the issue? Well, $\gamma$ is interpreted in the units of $Z$ instead of $D$, which is not what we’re interested in. Note, $\gamma = \partial Y / \partial Z$. So, what we need to do is translate $Z$ into $D$’s units. We can do that by estimating the first-stage regression. In this case, $\rho = \partial D / \partial Z$. Once we have this estimated model, we can use it to predict $\widehat{D_i}$ for each $Z_i$. This is just a prediction from a regression, like the fitted values you have seen before. This step allows us to re-estimate the reduced form equation with our new $\widehat{D}$ instead of $Z$, so we have the proper units. This will generate $\delta$, our causal effect, which is equal to $\gamma / \rho = \frac{\partial Y / \partial Z}{\partial D / \partial Z}$. ## IV Code Now that we’ve seen some of the math, let’s code up a quick simulation.

Feel free to experiment with these parameters if you’d like.

``` r N <- 200 draft <- sample(0:1, N, TRUE) personality <- sample(0:1, N, TRUE) # substract draft*personality to remove double counting military <- draft + personality - draft*personality earnings <- 3*military - 4*personality df <- data.frame(earnings = earnings, military = military, draft = draft, personality = personality) ``` - `draft` and `personality` are determined by random number generators. - `military` is equal to 1 either if `draft == 1` or `personality == 1`. - `earnings` is equal to `3*military - 4*personality`. ``` r # Tabulate draft status and military experience: table(draft = , military = ) ``` Notice how everyone who got drafted joined the military, though not all people who joined the military got drafted. This should be a clear indicator that draft status is not the only thing causing people to join the military. In terms of estimation, if we could observe this other factor (i.e. `personality`), we could control for it, and our estimate on `military` would be causal. Let’s demonstrate it. ``` r # Estimate "true" model lm( ~ , df) ``` We find a treatment effect of 3, which is what we specified in the simulation, so this works! However, we cannot typically observe/quantify personality, which presents a problem for us. What if we estimated the regression without it? ``` r # Estimate naive model without personality lm( ~ , df) ``` Without controlling for personality, our coefficient is biased downwards. This is because personality is negatively associated with earnings but positively associated with military. See [this discussion about omitted variable bias](https://alexcardazzi.github.io/econ311/module05/module05-03.html#omitted-variables) for more information. Let’s try incorporating our instrument by replace military with draft. ``` r # Estimate reduced form with draft instead of military lm( ~ , df) ``` The generated output represents our reduced form estimates. Again, this just means we’re skipping steps and throwing our instrument into the regression with our outcome of interest. While you will often see this equation estimated, it is not *really* part of the IV algorithm. Now, to estimate the IV model, we have to begin with our first stage. ``` r # Estimate first-stage where # military is explained by draft lm( ~ , df) # Save this regression as an object and # use summary() to explore the output! ``` Let’s think about this now. We get a coefficient of about 0.5. This suggests that being drafted increases the probability of enlisting in the military by 50%. Cool – it seems like our instrument is doing a good job at predicting our treatment. In just a minute, we’ll formalize “doing a good job”, but for now, let’s take it at face value. Our next step is to get the fitted values of military. Then, we will substitute *this* variable into the regression for our “real” treatment. Finally, estimate the parameters of the second stage: ``` r stage1 <- lm(military ~ draft, df) df$military_fitted <- stage1$fitted.values # Estimate second stage lm( ~ , df) # Save this regression as an object and # use summary() to explore the output! ``` Nice! Our slope coefficient is pretty close to 3, which is the true effect we established in the simulated data. As a note, here’s why the reduced form estimates are interesting. As mentioned, if we take the ratio of $\frac{\partial Y}{\partial Z}$ and $\frac{\partial X}{\partial Z}$, we will get the second stage coefficient. Let’s test this out: ``` r rf <- lm(earnings ~ draft, df) # dy/dz stage1 <- lm(military ~ draft, df) # dx/dz rf$coefficients[2] / stage1$coefficients[2] ``` ## Assumptions Great! Now we can mechanically estimate IV parameters! Well, wait a minute… there are a few things I skipped in this discussion. First, we still have assumptions that we need to be wary of. Second, there are some further technical considerations that we’ll touch on in the following sections. Let’s discuss the assumptions in IV. There are three main ones. **Relevancy**: The instrument must to be a good predictor of the treatment. Otherwise, there won’t be enough variation in the fitted treatment values to explain the outcome. When this happens, we have a *weak* instrument. Conveniently, this assumption is directly testable! To test if our instrument is relevant, we can calculate an F-statistic that indicates the strength of the instrument. As a rule of thumb, the F-statistic must be greater than 10 for relevancy. Of course, larger F-stats are preferred! In fact, there has been some discussion in [recent literature](https://arxiv.org/pdf/2010.05058.pdf) that says this rule of thumb is too lenient. For this class, we will use this rule of thumb, but be aware that this might be fairly liberal. In addition, it always helps to have good theoretical explanations for why your instrument is relevant. **Excludability**: The instrument must only impact the outcome through the influence of the treatment. This is why we needed to control for “something” and “else” earlier in the notes. Unfortunately, this assumption is inherently untestable and similar in spirit to that of the parallel trends assumption in DiD or the assumption that there are no confounding variables you’ve missed when controlling for observables. If you are going to use IV, you have to be ready to argue that your instrument is excludable until you’re blue in the face.

In my personal experience, people (i.e. the endogeneity-police) **love** to attack the excludability assumption when someone uses an IV. While it is as equally untestable as some DiD or PSM assumptions, it gets much more scrutiny for whatever reason.

**Monotonicity**: Basically, this assumes away the existence of defiers in the sample. In other words, as the value of the instrument grows, it can only increase the probability (or intensity) of treatment. In terms of the military draft, we assume that being drafted can *only* increase (or at least not decrease) the chance that you enlist in the military. ## Revisiting IV Code In our last code section, we estimated a bunch of different models, mashed them all together, and our causal effect magically appeared from the rubble. Luckily, our handy-dandy `fixest` package provides an easy way to estimate IV models: `feols(Y ~ X1 + X2 | FE1 + FE2 | D ~ Z, data)` where `Y` represents the outcome, `X1` and `X2` represent any controls you might have, `FE1` and `FE2` represent fixed effects, `D` represents the (endogenous) treatment variable, and `Z` represents the instrument. If you do not have fixed effects or controls, you can use `1` in place of `X` or `FE`. By default, this will return the second-stage regression. However, if you want to access the first-stage (and your regression object is called `r_iv`), you can use: `r_iv$iv_first_stage`. To test for relevancy, we must generate an F-statistic. There are many variations of F-statistics that people tend to use that are robust to different things, but these are outside the scope of this course. Rather, we are going to focus on just two: the standard one with no bells or whistles, and the Wald F-statistic. The differences between these is that the standard one assumes your errors are homoskedastic. This may or may not true, and the Wald statistic will adjust depending on your standard error correction. To generate these, we can use the following code: `fitstat(r_iv, type = "ivf")` or `fitstat(r_iv, type = "ivwald")`.

A particularly famous test for weak instruments is the Anderson-Rubin test. This generates an F-statistic *and* coefficient confidence intervals that are robust to weak instruments. Unfortunately, `fixest` does not contain a test for this, but the `ivDiag` package (which is built on top of `fixest`) contains a function for this called `AR_test`. Using this is straight forward: `AR_test(df, "earnings", "military", "draft", controls = NULL)`

Try experimenting with some of this below: ``` r library("fixest") r_iv <- feols() r_iv$iv_first_stage cat("\n##### ##### #####\n\n") r_iv ``` You might notice a difference in this regression output compared to our step-by-step one. You’ll likely notice that the standard errors in the second stage estimation are a bit larger. This is because the first stage fitted values themselves come from a regression, so we need to build in the first model’s uncertainty when calculating the second model’s uncertainty. Thankfully, `fixest` does this for us, so we don’t need to get into the nitty gritty, but you should be aware of this. IV estimation is unbiased but less efficient (larger variance) than OLS estimation. ## Treatment Effects Now that we’ve become familiar with a few different causal inference methods, it’s important to talk about the different types of treatment effects. There are a few different ones, and you will probably see different names for some of these when Googling, but these are the basic ideas. As I see it, There are four main treatment effect types. Before even getting to the four, we need to think about what we’re even doing with causal inference. We need to think about *individual treatment effects*. That is, everyone has some potential outcome when they’re treated ($Y^1$) and some potential outcome when they’re not ($Y^0$). Therefore, the individual treatment effect can be thought of as the difference of these two potential outcomes. If we wanted to summarize the distribution of individual treatment effects, we could take an average. This would give us our first type of treatment effect: the **Average Treatment Effect** (ATE). However, due to the fundamental issue of causal inference, we cannot observe both potential outcomes for each (or any) individual, making the average impossible to calculate. Instead, we have to settle for the **Average Treatment on the Treated** (ATT). The ATT is estimated by subtracting the average potential outcome for control units from the average potential outcome for the treated units. Of course, under randomization, the ATT = the ATE. Without randomization, we need a combination of controls and assumptions. Sometimes, we aren’t able to observe the true treatment status for individuals. Rather, we can only observe assignment to treatment. In fact, this is probably the most common situation. In the case of enlistment, earnings, and the draft, being drafted is similar to being assigned to treatment. Thinking back to the DiD module where the minimum wage was changed for some restaurants but not others, this law change represents being assigned to treatment. However, if a restaurant was already paying above the new minimum wage, the treatment should not really impact them. The same thing could be said for someone already planning on enlisting in the military being drafted. The difference in potential outcomes conditional on treatment assignment, and not treatment status, is called **Intent to Treat** (ITT). [Imbens and Angrist (1994)](https://doi.org/10.2307/2951620) discuss a fourth types of treatment effect they call the **Local Average Treatment Effect** (LATE). In the paper, the authors write about [Angrist (1990)](https://www.jstor.org/stable/2006669).

Quote from [Imbens and Angrist (1994)](https://doi.org/10.2307/2951620)

> Angrist (1990) uses the Vietnam-era draft lottery to estimate the > effect of veteran status on earnings. The instrument is the draft > lottery number, randomly assigned to date of birth and used to > determine priority for military conscription. The average probability > of serving in the military falls with lottery number. Condition 1 > \[*excludability*\] requires that potential earnings with and without > military service be independent of the lottery number. This is a > standard IV assumption which would be violated if, for example, > lottery numbers are related to earnings through some variable other > than veteran status. Condition 2 \[*monotonicity*\] requires that > someone who would serve in the military with lottery number k would > also serve in the military with lottery number 1 less than k, which > seems plausible. … **The average effect of veteran status identified > under Theorem 1 is for men who would have served with a low lottery > number, but not with a high lottery number.** \[emphasis my own\]

The idea is that LATE is the effect of treatment on specifically the compliers. We can also think of this as the ITT divided by the change in probability of treatment for a one unit change in the instrument. If this isn’t ringing any bells, let me put it differently with a bit of math: the ITT is $\frac{\partial Y}{\partial Z}$, and the change in probability of treatment is $\frac{\partial X}{\partial Z}$. Look familiar? This is exactly the IV estimate we found above: $\frac{\partial Y}{\partial Z} / \frac{\partial X}{\partial Z}$! ## IV in Reality Alright, so now that we’ve gone through this example ad nauseam, what are the real findings in [Angrist (1990)](https://www.jstor.org/stable/2006669)? In short, the study finds earnings reductions of about 15% for (white) veterans compared to observationally similar nonveterans. Remember, this is a LATE, not an ATE. So, what does this tell us? If the government wanted to compensate drafted individuals who would not have served in the military had they not been drafted, the LATE is more in line with what they’d be interested in. Of course, not every researcher can get social security data and a clean military draft for an instrument. Good instruments usually feel like they were pulled out of thin air. In order to satisfy the exclusion restriction, you often need something a bit off the wall. I encourage students to read (the short) [Section 7.2.2 in The Mixtape](https://mixtape.scunning.com/07-instrumental_variables#good-instruments-should-feel-weird) for a good discussion of “weird” instruments. What are some examples of weird instruments used by other economists? There are plenty, but I will only mention a few here in addition to some canonical, or popular, instrumental variable designs. [Levitt (2002)](https://pricetheory.uchicago.edu/levitt/Papers/LevittUsingElectoralCycles2002.pdf) investigates the casual effect of police on crime. At that point in the literature, it was a challenge to disentangle the effects of police on crime. Of course, as crime increases, a city might feel the need to increase their police presence. So, crime causes police and police cause crime. Clearly, there’s some weird dynamics going on, so we need a way to isolate, or identify, the cause of police on crime. Levitt used the number of fire fighters in a city to instrument for the number of police officers. These two things should be related due to variation in city budgets, citizen preferences, etc. However, the number of fire fighters should not be related to crime in any material way. Levitt found that an increase in the number of police reduced the amount of crime, which at the time, was not the consensus in the literature as it is now. [Dube and Harish (2020)](http://odube.net/wp-content/uploads/2020/08/Queens_Dube_Harish.pdf) look at the effects of female leadership on peace. The authors collected data on European conflicts and monarchies between the years 1480 and 1913, where Queens ruled about 18% of the time. The authors use two instruments to predict treatment (whether a female was in leadership). The first instrument is a binary variable equal to 1 if the previous leader’s first born child was male. The second instrument is a binary variable equal to 1 if the previous leader had a sister. The findings suggest that Queens, relative to Kings, had more aggressive war policies. This is an interesting paper and worth a look. [Gibson and Shrader (2018)](https://doi.org/10.1162/rest_a_00746) examine the effect of sleep on earnings. Of course, sleep and earnings are endogenously determined by personality, etc, which will bias the OLS coefficient. The authors use time of sunset to instrument for the amount of sleep individuals get. The findings suggest that an additional hour of sleep can increase earnings by between 1 and 5%. Some Canonical IVs: - **Month of Birth, Relative Age**: [Angrist and Krueger (1992)](https://doi.org/10.2307/2290263) - **Old Maps**: [Duranton and Turner (2011)](https://doi.org/10.1257/aer.101.6.2616); [Möller and Zierer (2018)](https://doi.org/10.1016/j.jue.2017.10.002) - **Leniency Designs**: [Dobbie *et al.* (2018)](https://doi.org/10.1257/aer.20161503); [Dahl *et al.* (2014)](https://doi.org/10.1093/qje/qju019) - **Bartik, Shift-Share Instruments**: [Breuer (2022)](https://doi.org/10.2308/JFR-2021-003) For some further reading, check out the following two papers. First, [Angrist and Krueger (2001)](https://doi.org/10.1257/jep.15.4.69). The journal this paper is published in, Journal of Economic Perspective, is very reader friendly. The authors discuss all things IV with only words (no equations!). Note, if you download this PDF, it will show as being almost 100 pages long. In reality, it is only 15-ish pages and the other 75 pages contain citations to articles that cite this one (i.e. it’s famous). Second, for history fans, check out [Stock and Trebbi (2003)](https://doi.org/10.1257/089533003769204416). This is probably the best whodunit I’ve come across in economics. There was much debate about who first used IV between a father and son. The authors do a great job of explaining how they uncover who was the founder. ## Obligatory NHK Videos \ \ \ \ \