Natural Experiments & Instrumental Variables

As-if random assignment, non-compliance, and the IV estimator

Merlin Schaeffer · Department of Sociology

2026-10-26

By the end of today you can …

1. recognise a natural experiment, “as-if random” assignment by nature, and why it trades a little internal validity for more external validity;

2. see how non-compliance turns an RCT into an intention-to-treat design, where the offer \(Z\) is not the treatment \(D\);

3. use an instrumental variable to recover the treatment effect for compliers (the Wald estimator \(\rho/\phi\)) and state the three IV assumptions.

Natural experiments

Part 1 of 3

Some of the most important “treatments” can never be randomised. But sometimes the world randomises them for us.

First research question of the day

What is the average causal effect of a terrorist attack on xenophobia?

It is claimed that attacks like 9/11 shift public attitudes. Can we show it, causally?

NYC, 11 September 2001

Flight 175 hits the south tower.

Photo: Robert J. Fisch.

NYC, 15 September 2001

Firefighter calls for rescuers.

Photo: Preston Keres.

Newcastle, May 2010

“Shut down the mosque” march.

Photo: lionheartphotography.

Most of them were born after 9/11 — ask who knows what happened, and why a whole generation of politics is said to have changed that day. The first two photos are the attack itself; the third is what is claimed to follow: far-right mobilisation against Muslims, here the English Defence League marching against a mosque. Today we test that claim causally, using a smaller attack one year later (Bali, 2002) as our natural experiment. Stress the phrase “average causal effect”: we want a cause, not a correlation. Sensitive topic — keep it factual.

We would need an RCT

If we could randomly assign exposure to terrorism, treatment and control groups would come from the same population. They would be alike on everything, including their untreated potential outcome \(Y_0\):

\[E[Y_{0i} \mid D = 1] = E[Y_{0i} \mid D = 0]\]

The selection-bias term would vanish and the raw difference would be the causal effect \(\kappa\).

\[\begin{aligned} & \underbrace{E[Y_{1i} \mid D=1] - E[Y_{0i} \mid D=0]}_{\text{Comparison between treatment and control group}} \\[1.2em] &= E[Y_{0i} + \color{#901A1E}{\kappa} \mid D=1] - E[Y_{0i} \mid D=0], \\[1.2em] &= \color{#901A1E}{\kappa} + \underbrace{E[Y_{0i} \mid D=1] - E[Y_{0i} \mid D=0]}_{\underbrace{0}_{\text{Selection bias (if randomization has worked)}}}, \\[1.2em] &= \underbrace{\color{#901A1E}{\kappa}.}_{\text{The average causal effect}} \end{aligned}\]

Recall Lecture 6: randomising equalises the two groups’ baseline \(Y_0\), so selection bias is zero and the raw difference is the effect κ. Click to bring in the derivation on the right and walk through it line by line.

But that is unethical!

Stanford Prison Experiment, 1971: “guards” with a blindfolded “prisoner”.

Photo: Philip Zimbardo.

Zimbardo randomly assigned student volunteers to be guards or prisoners in a mock prison. Guards humiliated and abused prisoners and the study was stopped after 6 of 14 planned days. Participants were traumatized and the researcher, acting as “superintendent”, let it escalate.

The Stanford Prison Experiment shows why ethics boards exist: randomly assigning people to harmful roles did real damage. Treating people with terrorism would be far worse, so an RCT is not an option here. This is a common and fundamental challenge in sociology. Many of the “treatments” we care about are things we can’t, or shouldn’t, manipulate. We need a different strategy: go hunting for randomisation the world already did for us.

But nature can randomise for us

The first natural experiment: John Snow traced the 1854 London cholera outbreak to a water pump. Because rival companies’ pipes were laid haphazardly, which water a household got was as-if random, that is, unrelated to their wealth or health.

John Snow, 1813–1858.

Plaque honouring Snow.

Photo: Tony Hisgett.

Cholera killed fast and turned its victims blue: a victim in the “blue stage”, and cholera deaths across England and Wales. Image: via UCLA Dept. of Epidemiology.

“Salus Populi Suprema Lex”: George Cruikshank mocks the Southwark Water Works for piping sewage-filled Thames water to London homes, 1832. Image: via UCLA Dept. of Epidemiology.

The Southwark Water Company’s works on the Thames, before 1845. Image: via UCLA Dept. of Epidemiology.

Snow (1856) cholera map, 1854.

Snow’s 1855 map of the “grand experiment”: districts supplied by the Southwark & Vauxhall (blue) vs. the Lambeth company (red), whose pipes were laid haphazardly side by side. Image: Cooper Hewitt, public domain.

A natural experiment: exposure to treatment vs. control is as-if random, decided by nature or by forces outside the researcher’s control.

The core idea: sometimes exposure is “as-if random” by nature. Snow, 1854 — rival water firms had laid their pipes haphazardly, so which water a house drank was unrelated to wealth or health. That let him compare death rates by supplier and pin cholera on one pump. The first natural experiment in history.

Today’s natural experiment: The Bali bombings, October 2002

Legewie (2013) spotted a natural experiment: the 2002 Bali attack struck during the European Social Survey’s fieldwork. Whether a respondent was interviewed before or after the attack was as-if random; so “after” is the treatment group, “before” the control.

Joscha Legewie, Harvard University

Under what conditions is this design valid?

1. Interview date is as-if random.
   \(\rightarrow\) Reachability bias: easy-to-reach people are interviewed earlier.
2. No other event moved attitudes at the same time.

Start with the photo and the Wikipedia page: 202 dead, many of them European tourists, front-page news across Europe. Click: Legewie’s move: the Bali attack landed mid-fieldwork in the ESS, so interview timing splits people into after (treated) and before (control). Point at the figure — control is the 30 days before, treatment the week after. Click: ask the class under what conditions this design is valid, and collect answers before revealing the two assumptions: interview date is as-if random (threat = reachability bias, easy-to-reach people are interviewed early), and no other big event hit at the same moment.

RCT vs. natural experiment

Internal validity: The estimated parameter, \(\beta_{I \rightarrow Y}\), really captures what the study claims it captures (e.g., a causal effect) in the study’s own sample and setting.

\(\rightarrow\) the RCT wins over the natural experiment, because the researcher controls assignment. The intervention \(I\) is therefore known to be random. We are sure no confounder \(C\) sneaks in.

External validity: The estimated parameter, \(\beta_{E \rightarrow Y}\), found in the study generalises to other people, places, times and real-world versions of the treatment.

\(\rightarrow\) The natural experiment wins over the RCT. We study a real event \(E\), not an artificial intervention; findings travel better. The price: we must assume \(E\) is as-if random (the “?” arrow), not know it.

Not a winner — a trade-off. RCT: we control assignment, so internal validity is high — we know it’s random. Natural experiment: a real event, so external validity is better — but we must assume the as-if-random arrow (the “?”), we can’t guarantee it. Both aim to shut the confounder \(C\) — one by design, one by argument.

How to

Photo: Robert Vayssié.

Finding a natural experiment, not the statistics, is the hard, creative part. They are rare as truffles. Are you a lucky truffle pig?

Learning goal 1: terror can raise xenophobia

Because the interview day is as-if random, Legewie estimates the causal effect of the Bali attack on anti-immigrant attitudes, country by country, with plain OLS.

What does the figure show? In which countries did the attack change anti-immigrant attitudes, and in which not?

The attack significantly raised xenophobia in Portugal, Poland & Finland — but had no detectable effect in Great Britain, the Netherlands, or Norway. The same shock, different societies: why is the next research question. You can find the answer in Legewie (2013).

Source: Legewie (2013)

The payoff. Point at the plot: significant rise in Portugal, Poland, Finland — nothing in the UK, Netherlands, Norway. Same shock, different societies — why? is the real sociological question (tell them to read the paper). And stress: the hard, creative part was spotting the natural experiment; the statistics are just weighted OLS.

Preparation: Legewie’s data in R

• Packages
• The attack window
• Prepare the data

pacman::p_load(
  tidyverse,       # Data manipulation and visualization
  haven,           # Read Stata (.dta) files
  estimatr,        # OLS with robust standard errors (and weights)
  modelsummary,    # Regression tables
  masteringmetrics # Data from Angrist & Pischke's book (exercise 2)
)

# Bali terror attack, and the ESS fieldwork window around it
event_date_begin <- as.Date("2002-09-14") # 30 days before
event_date       <- as.Date("2002-10-13") # The attack
event_date_end   <- as.Date("2002-10-20") # One week after

ESS <- read_dta("Legewie_ESS_02.dta") %>%
  mutate(
    int_date = sprintf("%s-%s-%s", inwyr, inwmm, inwdd) %>% as.Date(), # Interview day
    treat = case_when(                                         # Treatment indicator
      int_date > event_date & int_date <= event_date_end ~ "After the attack",
      int_date < event_date & int_date > event_date_begin ~ "Before the attack",
      TRUE ~ as.character(NA)) %>% fct_relevel("Before the attack", "After the attack"),
    anti_immi = rowMeans(select(., imtcjob, imbleco, imbgeco, imueclt, # Average of 7 items,
                                imwbcnt, imwbcrm, imbghct), na.rm = TRUE) %>%
      scale() %>% as.numeric(),                                # z-standardised,
    anti_immi = max(anti_immi, na.rm = TRUE) - anti_immi,      # high = xenophobic
    brncntr = as_factor(brncntr),                              # Born in the country?
    mocntr = as_factor(mocntr),                                # Mother born there?
    facntr = as_factor(facntr),                                # Father born there?
    pspwght = pweight * dweight) %>%                           # Weights
  filter(str_detect(cntry, "PT") &                             # Portugal, and only people
           brncntr == "yes" & mocntr == "yes" & facntr == "yes") %>% # without migration background
  select(treat, anti_immi, cntry, pspwght) %>%
  drop_na()

Walk the pipeline once, top to bottom, in plain words: the interview date decides the group, seven attitude items are averaged into one xenophobia index, and the sample is restricted to Portuguese respondents without a migration background. They copy exactly this code in exercise 1, so the point here is recognition, not memorisation. Name the three new helpers as they pass: read_dta() reads a Stata file, as.Date() turns text into a date, str_detect() asks whether a text contains a pattern.

Break

Your turn: exercise 1

You replicate Legewie: estimate the Bali effect for Portugal and Sweden, and make a coefficient plot; a real AJS-style analysis.

Open exercise 1 in a new tab ↗

Non-compliance & intention-to-treat (ITT)

Part 2 of 3

Even RCTs can run into a problem: you can offer a treatment, but you cannot force people to take it.

Second research question of the day

Does the neighbourhood you grow up in shape your future?

America’s inner cities in the 1970s: arson, abandonment, and whole blocks left in rubble.

What does growing up here do to a child?

Public housing, St. Louis, late 1960s.

Photo: USGS.

A burned-out tenement, South Bronx, 1980.

Photo: John Fekner.

A ruined building, South Bronx, 1980.

Photo: John Fekner.

Cleveland, 1973.

Photo: Frank J. Aleksandrowicz.

Set the scene before the study. In the 1970s the South Bronx lost tens of thousands of homes to arson and abandonment; President Carter’s 1977 visit to Charlotte Street made it a national symbol of urban decay. Pruitt-Igoe in St. Louis, the showcase public-housing project of the 1950s, was so run down by the 1970s that it was blown up (1972–76). Point at the Cleveland kids: this is the playground. Ask: what does growing up on a block like this do to a child’s life chances — and how could we ever answer that causally, when families who live here differ from families who don’t in countless ways?

Moving to Opportunity

One of the largest social-science RCTs ever. ~4,600 low-income families in high-poverty housing were randomly offered a voucher to move to a low-poverty neighbourhood. The question: does growing up in a poor neighbourhood hold children back?

Raj Chetty and colleagues followed the MTO children into adulthood (Chetty, Hendren, and Katz, 2016).

Robert Taylor Homes, Chicago, 1973: the kind of high-poverty public housing MTO offered a way out of. Photo: John H. White.

Gear change — this time a real RCT. The US government took ~4,600 poor families and randomly offered a voucher to move to a low-poverty area. The question: does your childhood neighbourhood set your destiny? Tease the catch coming next — they could offer the move, but not force it.

Voucher \(\neq\) move

But the lottery only randomised the offer, not the move. Families could decline or move anyway. So the randomly assigned \(Z\) (offer) is not the treatment \(D\) (actually moving).

You can offer the move; you cannot force it. A Chongqing “nail house” whose owners refused to leave, 2007. Photo: Zhou Shuguang.

Only compliers moved

Among families with young children who were offered the experimental voucher, only about 48% actually moved (Chetty, Hendren, and Katz, 2016).

This is (non-)compliance: the random \(Z\) (the offer) and the treatment \(D\) (moving) are not the same, \(|r_{Z,D}| < 1\); some move without a voucher, and some don’t move despite having won a voicher.

Take-up ≈ 0.4766. Source: Chetty, Hendren, and Katz (2016)

The snag: only ~48% of offered families actually moved. So the randomly-assigned thing (Z = the offer) is not the treatment (D = moving). Give it its name — non-compliance — and note it breaks the clean RCT logic we just relied on.

The intention-to-treat effect (ITT)

Compare everyone offered the voucher to everyone not offered, regardless of who moved. Because the offer was randomised, this intention-to-treat (ITT) difference is a clean causal effect: +$1,624 in adult earnings for kids whose parents were offered the move.

Because its randomized, its a causal effect;
but of what?

It is the causal effect of being offered the move \(Z\), not of actually moving \(D\). The kids of families who were offered a move, make (on average) $1,624 more than those who were not offered to move. This ITT of \(Z\) is a diluted effect of \(D\): an effect for the ~48% who moved, mixed with zero for the ~52% who stayed.

ITT ≈ +$1,624. Source: Chetty, Hendren, and Katz (2016)

The offer was random, so offered-vs-not is a clean causal effect: +$1,624. But push them: the effect of what? Of being offered, not of moving. It’s diluted — a big effect for the ~48% who moved, blended with zero for the ~52% who stayed.

RCT vs. intention-to-treat (ITT)

Full-compliance RCT: the intervention is the treatment. \[|r_{I,D}| = 1 \;\Rightarrow\; I = D\] The randomised difference is the treatment effect directly.

ITT / (non-)compliance: the offer only nudges the treatment. \[|r_{Z,D}| < 1 \;\Rightarrow\; Z \neq D\] The randomised offer injects some random variation into \(D\); enough to work with.

The injected random variation in \(D\) is exactly what an instrumental variable exploits.

Two correlations side by side: perfect RCT, intervention = treatment (|r| = 1); non-compliance, offer ≠ treatment (|r| < 1). The bridge line to Part 3: that leftover random wiggle the offer injects into \(D\) is exactly what an instrumental variable exploits.

Instrumental variables (IV)

Part 3 of 3

Use the randomly-assigned offer as an instrument to recover the effect of the treatment itself.

The cast of characters

Every IV argument juggles the same seven players.

Symbol	Role	In Moving to Opportunity
\(Z\)	Instrument — randomly assigned	the voucher offer (the lottery)
\(D\)	Treatment — what we care about	actually moving to a low-poverty area
\(Y\)	Outcome	the child’s adult income
\(C\)	Confounders	why we can’t just compare movers: ambition, family resources …
\(\phi\)	First stage \(Z \rightarrow D\)	offer → move \(= 0.48\)
\(\rho\)	Reduced form \(Z \rightarrow Y\) (the ITT)	offer → income \(= \$1{,}624\)
\(\lambda\)	What we want \(D \rightarrow Y\)	move → income \(= \rho/\phi \approx \$3{,}400\)

Slow down here — this is the anchor. Map every symbol to MTO out loud: Z = the offer, D = moved, Y = income, φ = 0.48, ρ = $1,624, λ = what we want. Tell them to keep this table in their heads; everything that follows is just these seven letters.

An instrument, and its three demands

Goal: the causal effect \(\lambda\) of the treatment \(D\) on outcome \(Y\).

Three requirements for an instrument \(Z\):

1. First stage: \(Z\) has a real effect \(\phi\) on \(D\) (testable).
2. As-if random: \(Z\) is unrelated to confounders \(C\) (in the MTO by design).
3. Exclusion restriction: \(Z\) affects \(Y\) only through \(D\) (not testable!).

Three tests for a good instrument. (1) First stage — does Z actually move D? This one is testable (the offer did cause moves). (2) As-if random — true here by the lottery. (3) Exclusion restriction — Z reaches Y only through D. Flag #3 now as the hard, untestable one; we unpack it next.

The exclusion restriction is fragile

Winning the lottery clearly makes families: 1. move (first stage ✓) 2. it was random (✓) \(\rightarrow\) two boxes ticked.

Discuss: could the random offer still reach a child’s income through some other path than moving — and so ruin the instrument?

Yes — for example if winning also sparked optimism that lifts earnings, whether or not the family moved. Then \(Z\) reaches \(Y\) through a second path: the exclusion restriction breaks. It is the one requirement you cannot test — you must argue it is implausible.

A violated exclusion restriction

The crux — and the assumption students confuse with “as-if random”. Ask the blue question first, give them a moment, then reveal: winning → optimism → income directly, bypassing the move. Hammer the point — you can never test this, you can only argue it’s implausible. This is where IV papers live or die.

Why divide? The dilution intuition

The offer only moved 48% of families. So the offer’s effect on income, the $1,624 ITT, is a diluted effect of moving: a gain for the ~48% who moved, blended with zero for the ~52% who did not.

To undo the dilution, scale it back up by the share who actually moved: \[\lambda = \frac{\$1{,}624}{0.48} \approx \$3{,}400\]

In one line: a weak nudge that still shifted incomes must mean each real mover was affected a lot. Dividing the (small) reduced form by the (small) first stage recovers that full per-mover effect.

If everyone had complied (\(\phi = 1\)), the ITT would be the treatment effect — no scaling needed. Non-compliance is exactly why we divide.

Build the intuition before the algebra. The offer moved only 48%, so its $1,624 effect on income is a diluted version of the real move-effect. Scale it back up — divide by 0.48 — to get ~$3,400. One line to say aloud: a weak nudge that still shifted incomes means each actual mover must have gained a lot.

The Wald IV estimator: a ratio

Two effects we can estimate cleanly, because \(Z\) is random:

First stage — \(Z\)’s effect on the treatment \(D\): \[\phi = E[D \mid Z{=}1] - E[D \mid Z{=}0]\]

Reduced form — \(Z\)’s effect on the outcome (the ITT): \[\rho = E[Y \mid Z{=}1] - E[Y \mid Z{=}0]\]

If \(Z\) works only through \(D\), then \(\phi \times \lambda = \rho\), so: \[\lambda = \frac{\rho}{\phi} = \frac{\text{reduced form}}{\text{first stage}}\]

For MTO: \(\lambda = \dfrac{\$1{,}624}{0.4766} \approx \mathbf{\$3{,}400}\) — the effect of moving for those who move because of the offer.

Now formalise: first stage φ, reduced form ρ, and λ = ρ/φ. Same $3,400 as the last slide — this is just that intuition written as algebra. If it helps, read it as “the outcome effect of the offer, undone by how much the offer actually shifted the treatment.”

Why a broken exclusion restriction is dangerous

Suppose the offer to move also affects income by some path \(\delta\) that bypasses moving out of the high-poverty neighborhood (e.g. optimism). Then the reduced form mixes two things: \[\rho = \underbrace{\phi \times \lambda}_{\text{through } D} + \underbrace{\color{#901A1E}{\delta}}_{\text{the leak}}\]

The Wald estimator divides all of \(\rho\) by \(\phi\): \[\frac{\rho}{\phi} = \lambda + \color{#901A1E}{\frac{\delta}{\phi}}\]

Intuition: dividing by \(\phi\) scales the ITT up to “what if everyone had complied”. But \(\delta\) works for everyone offered, complying mover or not, so scaling it up by \(\frac{1}{\phi}\) blows it up too. We additionally weigh up every other effect of \(Z\) by \(\frac{1}{\phi}\).

MTO in numbers: say winning the lottery adds just $200 to income directly. IV then reports \[\lambda + \frac{\$200}{0.48} \approx \lambda + \mathbf{\$420}\] The leak, \(\delta\), is more than doubled. With a weak first stage, say \(\phi = 0.1\), the same $200 becomes $2,000 of fake effect.

This makes the last slide’s warning concrete. Write ρ = φλ + δ on the board: the reduced form is the effect through moving plus any leak. Click: the Wald estimator divides the whole thing by φ, so we get λ + δ/φ. Click: the intuition — dividing by φ is how we scale a diluted ITT up to the compliers, but the leak was never diluted, it hit everyone who won the lottery; scaling it up inflates it. Click: the numbers. A small $200 leak becomes $420 with MTO’s φ = 0.48, and $2,000 with a weak instrument. Punchline: the weaker the first stage, the more a tiny exclusion violation contaminates the IV estimate — another reason to argue the exclusion restriction carefully and to want a strong first stage.

IV is LATE: only valid for compliers

The instrument only moves the compliers, people who take the treatment because they were assigned it. So IV recovers a Local Average Treatment Effect: \[\lambda = E[Y_{1i} - Y_{0i} \mid \text{complier}]\]

• Why only compliers? Never- and always-takers do the same thing whether offered or not; the offer shifts neither their \(D\) nor their \(Y\), so they add nothing to \(\rho\) or \(\phi\) and cancel out of the ratio. Only compliers are left.
• Monotonicity: assume no defiers (people who do the opposite of their assignment). Almost always reasonable.

Why a new letter? In Lecture 6 an RCT gave us \(\kappa\) — the effect for everyone. An instrument is weaker: \(\lambda\) is the same kind of causal effect, but only for the compliers. Same idea, narrower population — hence \(\lambda\), not \(\kappa\).

The twist nobody expects: IV speaks only about compliers. Walk the tree. Why? Never- and always-takers do the same thing regardless of the offer, so the instrument shifts neither their D nor their Y — they cancel out of both ρ and φ. Monotonicity = assume no “defiers” who do the opposite; almost always reasonable.

Learning goal 2: neighbourhoods matter

Instrumenting the move with the random voucher offer, Chetty, Hendren, and Katz (2016) recover the effect of actually moving as a young child: about +$3,477 in annual adult earnings.

Growing up in a low-poverty neighbourhood causally raises children’s later earnings \(\rightarrow\) place shapes destiny, for the compliers whose move the lottery caused.

IV / treatment-on-treated ≈ +$3,477. Source: Chetty, Hendren, and Katz (2016)

Payoff number two: instrument the move with the random offer, and moving out as a young child raises adult earnings by ~$3,477 (the treatment-on-treated column). Strong causal evidence that place shapes destiny — but keep them honest: this is the effect for the compliers, the families whose move the lottery actually caused.

Preparation: the Minneapolis data

The Minneapolis Domestic Violence Experiment. Sherman and Berk (1984) randomly told officers how to respond when called to intervene in a domestic violence case — but officers did not always comply.

# The data ship with the masteringmetrics package
data("mdve", package = "masteringmetrics")
mdve <- mdve %>%
  mutate( 
    T_RANDOM = case_when( # What officers were TOLD to do
      T_RANDOM == 2 | T_RANDOM == 3 ~ "Coddle!",
      T_RANDOM == 1 ~ "Arrest!",
      TRUE ~ as.character(NA)),
    T_FINAL = case_when( # What officers actually DID
      T_FINAL == 2 | T_FINAL == 3 ~ "Coddled",
      T_FINAL == 1 ~ "Arrested",
      TRUE ~ as.character(NA)))

mdve %>%
  select(T_RANDOM, T_FINAL) %>%
  table() # Cross-tabulate: who complied?
#          T_FINAL
# T_RANDOM  Arrested Coddled
#   Arrest!       91       1
#   Coddle!       45     177

Discuss: which cells are the compliers? And who are the others?

Domestic violence (staged, make-up). Photo: Commonpersoon, CC0.

A Copenhagen Police patrol car. Photo: Dk-2100, CC BY-SA 3.0.

Read the cross-table with them: the diagonal cells, told to arrest and arrested, told to coddle and coddled, are the compliers. The off-diagonal cells are officers who did something else than the lottery said. This is the same non-compliance as in MTO, now as a table they can compute themselves — table() is the one new function, and it simply counts every combination.

Your turn: exercise 2

Does arresting domestic-violence suspects deter repeat offences? The Minneapolis experiment had non-compliance too. You compute the IV estimate yourself.

Open exercise 2 in a new tab ↗

Today’s general lessons

1. A natural experiment exploits as-if random exposure created by nature; less control than an RCT, but real events and better external validity.

2. With non-compliance, the randomised \(Z\) is not the treatment \(D\). The intention-to-treat effect is the clean causal effect of \(Z\), diluted by everyone who didn’t comply.

3. An instrumental variable uses the random \(Z\) to recover the treatment effect \(\lambda = \rho/\phi\), if the first stage is real, \(Z\) is as-if random, and the exclusion restriction holds.

4. IV estimates a LATE: the effect only for compliers, assuming no defiers (monotonicity). It is silent about never- and always-takers.

Recap the four ideas: natural experiment (nature randomises), ITT (the effect of the offer), IV (recovers the treatment effect as ρ/φ), LATE (compliers only). Tie it together: the whole day was about finding — or engineering — random variation to shut the confounder C.

Check yourself: today’s goals

• Explain why an interview date, or a lottery, can serve as “as-if random” assignment, and what could break that.
• Say why the ITT effect of being offered a move is not the effect of moving, and what non-compliance does to \(r_{Z,D}\).
• Compute an IV estimate as reduced form ÷ first stage, and state whose effect (which group) it is.

Shaky on any of these? That is what this week’s Absalon quiz and the Friday exercise class are for.

Today’s important functions

• estimatr::lm_robust(y ~ z, weights = ...): the reduced form (\(\rho\), effect of the offer) and — with the treatment as the outcome — the first stage (\(\phi\)).
• The Wald estimator is then just arithmetic: lambda <- rho / phi. No special function needed.
• haven::read_dta(): read a Stata (.dta) file, such as Legewie’s ESS data.
• as.Date(): turn text like "2002-10-13" into a date you can compare with < and >.
• str_detect(x, "PT"): does a text contain a pattern? Handy in filter().
• table(): cross-tabulate two variables, e.g. assigned vs. actual treatment.
• masteringmetrics::mdve: the Minneapolis domestic-violence experiment (exercise 2).
• (Soon) ivreg::ivreg(y ~ d | z) runs the first stage, reduced form and division in one step — 2SLS.

References

Chetty, R., N. Hendren, and L. F. Katz (2016). “The Effects of Exposure to Better Neighborhoods on Children: New Evidence from the Moving to Opportunity Experiment”. In: The American Economic Review, pp. 855-902.

Legewie, J. (2013). “Terrorist Events and Attitudes toward Immigrants: A Natural Experiment”. In: American Journal of Sociology, pp. 1199-1245.

Sherman, L. W. and R. A. Berk (1984). “The Specific Deterrent Effects of Arrest for Domestic Assault”. In: American Sociological Review, pp. 261-272.

Snow, J. (1856). “On the Mode of Communication of Cholera”. In: Edinburgh Medical Journal, pp. 668-670.