How to use this guide

• One lecture per tab. Only one is on screen at a time. Every lecture follows the same five steps (below), so you always know where you are.
• Yellow box first. Each lecture opens with the 3 things to remember, then what you'll be able to do afterwards, each marked Foundational, Intermediate or Advanced.
• "Just the gist" (top right) hides the sections marked deeper. Use it for a first pass, then switch to Full.
• Explain buttons. Tricky ideas have Simple / Intuitive / Technical switches, so you can change the depth of one concept without changing the whole page.
• Play with the demos. Each lecture has an interactive simulation: move a slider and see why a result changes.
• Practise, don't just read. "Apply" and "Challenge" questions give feedback on the exact answer you picked. Exam mode mixes questions from all lectures, with a timer if you want one.
• Final test when everything is studied: thirty new questions, graded together, then a score per lecture and a study plan that links to the exact sections to revisit.
• Search (top right, or press /) looks through everything: definitions, explanations, questions and R code.
• Optional R labs show each method on real-looking data, with the exact output you should get and downloadable scripts.
• Your progress stays in this browser only.

The five steps in every lecture

1. UnderstandPlain-language explanation and a worked example.
2. See itAn interactive demo: change something, watch what happens.
3. ApplyShort calculations and output-reading questions.
4. ChallengeSpot the broken assumption or the wrong conclusion.
5. ReviewQuick recall questions, then exam mode later.

Your progress

Studied = you ticked it. Practised = you answered every Apply and Challenge question. Mastered = at least 80 % right in exam mode on most of that lecture's questions, or at least 80 % on that lecture's part of the final test. Mastered lectures show "review due" after a week, because recalling something a few days later is what makes it stick.

The map

Five words you'll see everywhere

What is regression for?

Two very different jobs:

Keep asking yourself which job you're doing. Many rules in this lecture change depending on the answer.

The model, in words

What the line is aiming at: the conditional expectation

E[Y | X = x] is the average of Y among everyone with that value of x: the average wage of people with 12 years of school, of people with 13 years, and so on. Plot those averages and you get the conditional expectation function (CEF).

• If the CEF is a straight line, regression recovers it exactly (in large samples).
• If it's curved, OLS gives the best straight-line approximation to it. That's still useful, but check with a plot.
• The error ε is "Y minus its conditional average". The assumption E[ε | X] = 0 says the line gets the averages right for every x.

This is a statement about averages among people who differ in X. Whether changing someone's X would change their Y is a different, causal question (lecture 4).

Least squares: how the line is chosen

Geometrydeeper
Fitting OLS = dropping a perpendicular from y onto the space spanned by the columns of X. The fitted values ŷ = Py are the "shadow" of y (P is the projection matrix). The residuals ε̂ = My are what's left (M = I − P is the residual maker). Both P and M are symmetric and idempotent (doing them twice changes nothing), and ŷ is perpendicular to ε̂.

Why OLS is a good choice: the Gauss–Markov theorem says that if the model is linear in β, X has full rank (no perfect collinearity), errors average zero given X (exogeneity), and errors have constant variance and are uncorrelated with each other, then OLS has the smallest variance of all linear unbiased estimators. Short name: BLUE (Best Linear Unbiased Estimator). Normal errors are not needed for BLUE; they're only needed for exact small-sample t and F tests.

"Linear" doesn't mean "straight"

Linear means linear in the β's. You can transform the x's and y however you like:

• log(y) = β₀ + β₁x + β₂x² + ε is still a linear model (a curve!).
• y = β₀ · x^β₁ · ε becomes linear after taking logs: log y = log β₀ + β₁ log x + log ε.

R²: how much variation the line explains

Reading the coefficients (the log table)

This shows up on exams all the time. Learn this table:

Interaction termsdeeper
log(wage) = β₀ + β₁educ + β₂south + β₃south·educ + ε. Outside the South the education slope is β₁. In the South it is β₁ + β₃ and the intercept shifts by β₂. So β₃ answers "is the return to education different in the South?"

What can go wrong

1 · Omitted variable bias (the big one)

True model includes ability, but we can't measure it:

Which variables to control for (lecture 4) →

Related: Simpson's paradox. Adding one variable can flip the sign of another coefficient. So two models can give completely different β̂₁.

2 · Collinearity

When x's are strongly correlated with each other, OLS can't tell them apart. Estimates get high variance and become unstable.

• Spot it: correlations near ±1; regressing xⱼ on the other x's gives Rⱼ² near 1; condition number √(λ₁/λ_p) ≥ 30.
• Measure it: variance of β̂ⱼ is multiplied by 1/(1 − Rⱼ²), the variance inflation factor.

3 · Heteroskedasticity

"Hetero" = different, "skedastic" = spread. The errors are bigger for some x's than others (e.g. y = 1 + 3x + x·ε: bigger x, bigger noise). The usual standard-error formula assumed constant spread σ².

Heteroskedasticity does not bias β̂ (as long as errors still average zero given X). What breaks is the conventional standard errors, and with them t-tests and confidence intervals.

• Fix A, weighted least squares: give noisy points less weight, wᵢ = 1/var(yᵢ). Example: if yᵢ is an average over nᵢ people, use wᵢ = nᵢ.
• Fix B, robust standard errors (HC0–HC3): keep OLS β̂, fix only the standard errors. Angrist & Pischke prefer this one.

4 · Clustered errors

People in the same school or town share shocks. Cluster your standard errors when treatment is assigned at group level, or when you sampled groups first and people second.

See it: the regression playground

Fifty made-up people. The dashed orange line is the true relationship used to create the data. The solid blue line is what OLS estimates from this one sample. Change one thing at a time and watch what moves.

What p-values and CIs actually mean

Your lecturer spends several slides on this, so expect it in an exam.

The coin example

You flip a coin 500 times and get 97 heads and 403 tails. Is it fair?

If p = 0.5, seeing exactly 97 heads has probability about 9.3 × 10⁻⁴⁶. Basically impossible. So which p fits best?

See it: the likelihood explorer

Choose how many flips and heads you saw. The curve shows how well each p explains those data (log-likelihood, with the top set to 0). Drag your guess and read the slope (the score): it points towards the top.

The shaded band marks the p values within 1.92 log-points of the top: a likelihood-based 95 % interval. Keep the share of heads fixed and raise n: the hill gets sharper and the band and SE shrink. That sharpness is the Fisher information.

The recipe

1. Pick a distribution for your data with an unknown parameter θ: f(x | θ).
2. Write the likelihood. With independent (i.i.d.) observations it's a product: L(θ) = f(X₁|θ) · f(X₂|θ) · … · f(Xₙ|θ). Independence is what lets you multiply.
3. Take logs: ℓ(θ) = Σ log f(Xᵢ|θ). Same maximum, numerically more stable.
4. Set the derivative (the score) to zero and solve. If there's no formula, a computer climbs the hill numerically.

Waiting-time example (exponential)

100 waiting times between insurance claims. Model: exponential with mean λ, f(x|λ) = e^(−x/λ) / λ.

Challenger: why logistic regression needs ML

Each shuttle launch had 6 O-rings; some failed. We want the failure probability pᵢ as a function of temperature.

• A straight line pᵢ = β₀ + β₁·temp can predict probabilities below 0 or above 1. Bad.
• Fix: model the log-odds, log(pᵢ/(1−pᵢ)) = β₀ + β₁·tempᵢ. Any β gives a p between 0 and 1.
• Randomness: failures yᵢ ~ Binomial(6, pᵢ). Now the model is fully described except for β₀, β₁.
• Likelihood: multiply C(6,yᵢ)·pᵢ^yᵢ·(1−pᵢ)^(6−yᵢ) across launches, take logs, and let the computer find the β's that maximise it.

Why people love MLE

• Consistent: θ̂ → true θ as n grows (needs i.i.d. data, identification and some regularity conditions).
• Asymptotically normal: you can build t-tests and confidence intervals.
• Asymptotically efficient: it hits the Cramér–Rao lower bound, the smallest variance any unbiased estimator can have: Var(θ̃) ≥ (nJ)⁻¹.
• Invariant: if θ̂ is the MLE of θ, then h(θ̂) is the MLE of h(θ). Example: the MLE of p² is p̂².

Link back to lecture 1

If y = Xβ + ε with normal errors, the log-likelihood is a constant minus (1/2σ²)·Σ(yᵢ − xᵢβ)². Maximising it is the same as minimising the sum of squared residuals.

Back to least squares in lecture 1 →

So OLS = MLE when errors are normal. (Small difference: MLE estimates σ² = ε̂ᵀε̂/n, dividing by n instead of n − p.)

Try it yourself

Here are 9 waiting times (days between insurance claims). The estimate is the mean. Press the buttons and watch the bootstrap distribution build up.

Notice: the histogram of means is much narrower than the data itself, and it's lopsided because two big values (13.95, 18.03) drag some resamples up. A normal approximation would miss that lopsidedness. But with only 9 values, the whole picture rests on those 9 numbers: the bootstrap can't tell you about values you never observed.

Use the menu to swap in a fresh sample of 9, 30 or 100 from a skewed population whose true mean is 5. Then press Repeat the whole study: it checks how often the "95 %" interval really contains 5. With 9 values it falls clearly short; with 100 it gets close.

The algorithm

1. Draw a sample of size n from your data (the empirical distribution F̂ₙ), with replacement.
2. Compute your statistic on it: T*.
3. Repeat B times (say 1,000–10,000).
4. Use the B values of T*: their standard deviation = SE, their percentiles = CI, their mean minus the original = bias estimate.

The key logic: F̂ₙ is close to the true F, so how estimates vary when sampling from F̂ₙ is close to how they vary when sampling from F. More resamples B only make the simulation more accurate; they don't add real information.

When to reach for it

• Moderately small samples where "large n" formulas are shaky (e.g. n = 30–50 with skewed data), provided the sample still represents the population reasonably well.
• Complicated estimator with no known formula for its variance (e.g. the output of a numerical optimisation).
• Formula depends on unknowns. The sample median's variance is 1/(4n·f(m)²), which needs the unknown density f at the median.
• Dubious assumptions, e.g. stock returns with fat tails, where normality is wrong.

When the bootstrap fails

• Parameter on the boundary. E.g. X ~ N(μ, 1) but μ is only allowed to be ≥ 0, and the true μ = 0 (Andrews, 2000).
• Sample maximum. If data are uniform on [0, θ], the bootstrap max equals the sample max with probability 1 − (1 − 1/n)ⁿ → 1 − 1/e ≈ 63 %. The real sampling distribution has no such spike. So the bootstrap gets it wrong.
• The paradox: we want the bootstrap in complicated situations, but those are exactly where it's hardest to prove it works.

Fix: subsampling. Draw smaller samples (size m < n) without replacement. Works more generally, but is less efficient when the normal bootstrap works, and you have to choose m.

Correlation ≠ causation

The 2021 Economics Nobel (Card, Angrist, Imbens) went to the "credibility revolution": methods for getting causal answers from real-world data. This lecture is the trailer for the rest of the course.

Potential outcomes

Imagine we could see both versions of each person:

In reality, half the cells are missing. If Adam is treated, we see his 4 and never his 6. If Cyril isn't, we see his 6 and never his 8. Individual effects are never observed.

Why a naive comparison misleads: selection bias

Without randomisation, comparing the treated with the untreated mixes two things:

See it: coin flip vs choosing for yourself

Two hundred simulated people, each with a Y(0) and a Y(1). The true average effect is about 5. Assign treatment by coin flip, or let people choose: those with a high Y(0) are more likely to sign up.

Statistical vs causal inference

A very precise estimate (tiny SE) can still be the wrong kind of number. Precision and credibility are separate questions; always answer both.

What to control for: confounders, mediators, colliders

"Add more controls" is not always safer. It depends on where a variable sits in the causal picture (a DAG, directed acyclic graph: arrows mean "causes").

The problem: we usually can't randomise

Questions where a proper experiment is impossible or unethical:

• Do veterans earn less because of the war?
• Does education increase wages?
• How does the minimum wage affect unemployment?
• Does class size affect learning? Does alcohol cause car crashes?

Option 1: compare similar people, Y(1), Y(0) ⫫ D | X ("random once we control for X"). Works only if you've measured everything that matters.

Option 2: find a source of randomness, a "quasi-experiment".

The quasi-experiment idea

Some Z (a lottery, a birth date, the weather) pushes the treatment D, and touches Y only through D:

See the IV formulas in lecture 5 → · How IV, RDD and DiD fit together →

Famous examples (you'll meet them again)

The problem: endogeneity

D is endogenous (correlated with the error) when there is:

• an omitted variable U,
• reverse causality (Y also affects D),
• or measurement error in D.

Then the OLS condition E[D·η] = 0 fails and OLS is biased.

The three (four) conditions

Independence + exclusion together = validity: E[Z·η] = 0.

The formulas

Where the formulas come from: method of momentsdeeper
Write down conditions that hold at the true value, then solve their sample versions. For a mean: E[Y − μ] = 0 ⇒ μ̂ = Ȳ. For OLS: residuals average zero and are orthogonal to D, giving Cov(D,Y)/Var(D). For IV: keep "residuals average zero", but replace the second condition with residuals orthogonal to Z, Σ Zᵢ(Yᵢ − α − δDᵢ) = 0. Demean and solve: δ̂ = Cov(Z,Y)/Cov(Z,D). We weight by Z because E[Zη] = 0 is believable, while E[Dη] = 0 is exactly what fails.

Two-stage least squares (2SLS)

1. First stage: regress D on Z (and controls X). Save the fitted values D̂.
2. Second stage: regress Y on D̂ (and the same X, but not Z).

The slope on D̂ equals the IV ratio exactly.

Controlsdeeper
If X affects both Z and Y, Z is only valid given X, so X goes in both stages. Equivalent trick (Frisch–Waugh–Lovell): regress Y, D and Z each on X, keep the residuals, then apply the simple formula Cov(Z⊥, Y⊥)/Cov(Z⊥, D⊥). "Controlling for X" = removing X from everything, then using what's left.

Weak instruments

Rewrite: δ̂_IV − δ = Cov(Z, η) / Cov(Z, D). If Z barely moves D, the bottom is near zero, so tiny noise on top gets blown up. The estimate becomes erratic, and conventional standard errors and t-tests stop being trustworthy.

Which way does it go wrong? In the textbook setting (one endogenous D, conventional 2SLS, Z truly valid), the finite-sample distribution of 2SLS tends to be centred towards the OLS estimate, because with little clean variation the estimate is dominated by the same contaminated variation that biases OLS. This is a common pattern, not a universal law: with many instruments it gets worse, with just-identified IV the estimator may not even have a finite mean, and if Z is also slightly invalid, a weak first stage magnifies that bias in any direction.

Old rule of thumb: first-stage F-statistic of at least 10. Newer work (Lee, McCrary, Moreira & Porter 2022) shows the usual ±1.96 t-test needs F around 104 to be reliable. With a weaker first stage, use weak-instrument-robust inference such as Anderson–Rubin confidence intervals.

See it: strong, weak and invalid instruments

Each press runs 500 imaginary studies with 200 people. A hidden U raises both D and Y, so OLS is biased. The true effect of D is 0.5. Make the instrument weaker, or let it affect Y directly (breaking exclusion), and watch the IV estimates.

LATE: who does IV tell us about?

In real experiments people don't always follow their assignment (imperfect compliance). Comparing by assignment gives the ITT (intention-to-treat): the effect of being offered treatment.

Always- and never-takers do the same thing whatever Z is, so they add nothing to the reduced form. All of it comes from compliers. So reduced form ÷ first stage = average effect for compliers, the LATE.

Two words for non-compliance: treatment migration (controls get treated anyway) and treatment dilution (assigned people don't take it).

The picture is the method

Imbens & Lemieux: if the basic plot shows no jump, fancy regressions are unlikely to find a credible one. Always start with the plot.

Sharp RD

Identifying assumption, continuity: the average potential outcomes E[Y(0)|X] and E[Y(1)|X] change smoothly through c. Without treatment, there would be no jump. So:

Threats: when people game the cut-off

Estimating it

• Global polynomials (fit the whole range with x, x², x³…): avoid high orders. Far-away points get big, erratic weight. In the slide's simulation (true τ = 1), estimates ranged from 0.55 to 2.2 depending on the polynomial order (Gelman & Imbens 2019).
• Local linear (recommended): use only points with |X − c| ≤ h (the bandwidth), fit a line on each side, and weight closer points more (triangular kernel).

See it: the bandwidth simulator

Six hundred simulated people. Treatment switches on at X = 0 and the true jump there is 0.4. The relationship curves, and differently on each side, so wide windows can mislead. The shaded window is the bandwidth; blue points are the ones used.

Fuzzy RD = IV at the cut-off

Sometimes crossing c only raises the chance of treatment. E.g. students scoring below 80 are eligible for free tutoring, but some don't go and some above 80 find a way in.

Revisit the Wald estimator in lecture 5 →

Assumptions: relevance (eligibility shifts take-up, testable), exclusion (crossing 80 matters only through tutoring; it fails if being labelled "below 80" discourages students), monotonicity.

Case study: Austrian parental leave

Lalive & Zweimüller (2009). From 1 July 1990, parental leave was extended from 1 to 2 years. Running variable = child's date of birth. Compare June 1990 mothers (control) with July 1990 mothers (treated).

John Snow and the cholera "Grand Experiment"

London, 1850s. In 1852 the Lambeth water company moved its intake upriver, above the sewage. Southwark & Vauxhall (S&V) kept taking dirty water. Both companies' pipes ran down the same streets, so neighbours breathed the same air but drank different water.

The picture

See it: when parallel trends hold, and when they don't

Six periods, policy from period 0. The dashed orange line is the counterfactual DiD assumes: the treated group continuing on the control group's path. Make the treated group drift on its own and see the estimate go wrong.

The 2 × 2 setup and its assumptions

The target is the ATT: average effect on the treated group after treatment. It's identified under three assumptions:

• Consistency / SUTVA: observed outcome = potential outcome under the treatment received. Treatment is well defined, and there are no spillovers onto the control group.
• No anticipation: the treated don't react before treatment starts (e.g. to an announced policy).
• Parallel trends: E[Y₁(0) − Y₀(0) | treated] = E[Y₁(0) − Y₀(0) | control]. The only assumption about the unseen counterfactual.

The derivation in three stepsdeeper
(1) Add and subtract the treated group's "before" outcome, so ATT = (actual change of treated) − (untreated change of treated, unknown). (2) Parallel trends replaces that unknown change with the control group's change. (3) Consistency + no anticipation turn every potential-outcome term into an observed mean. Result: ATT = (μ₁,₁ − μ₁,₀) − (μ₀,₁ − μ₀,₀).

Event studies: checking pre-trends

Replace the single "treated × after" dummy with one dummy per period relative to treatment, k = t − (adoption time). Leave out k = −1 as the reference.

• Leads (k < 0): should be near zero. If not, trends weren't parallel before.
• Lags (k ≥ 0): how the effect evolves. The slides' fracture example shows income dropping by over €500/month at month 2 and slowly recovering. One average number would hide that.

Staggered adoption: why TWFE breaks

Many groups, treated at different times. The usual regression is two-way fixed effects: Yᵢₜ = αᵢ + λₜ + β·Dᵢₜ + uᵢₜ (unit FE + time FE).

Goodman-Bacon (2021): β_TWFE is a weighted average of every possible 2×2 DiD in the data:

1. early-treated vs never-treated ✓
2. late-treated vs never-treated ✓
3. early vs late (late still untreated) ✓
4. late vs early, using the already-treated early group as control ✗

If effects grow over time, the early group keeps changing after treatment. Using it as a "control" subtracts that growth. The estimate can even flip sign.

The fix: Callaway & Sant'Anna

Rule: never use already-treated units as controls. For each cohort g (first treated in period g) and each later period t, compute a clean 2×2 DiD called ATT(g, t):

• Treated change: cohort g from s = g − 1 (last pre-period) to t.
• Control change: units not yet treated at t (or never treated), over the same s → t.

deeper Then aggregate: by event time (dynamic profile), by calendar time, or overall (average within each cohort first, then across cohorts weighted by size; a plain average over cells overweights early cohorts). Related estimators: Sun & Abraham (2021), de Chaisemartin & D'Haultfœuille (2020, who show TWFE can put negative weights on some ATT(g,t)). Overview: Roth et al. (2023).

Standard errors

Outcomes of the same unit are correlated over time, so ordinary SEs are far too small (Bertrand, Duflo & Mullainathan 2004). Cluster at the level where treatment is assigned (e.g. state). With very few treated clusters (one state!), even clustered SEs are unreliable.

Clustered errors in lecture 1 →

Case study: minimum wage (Card & Krueger 1994)

• April 1992: New Jersey raised the minimum wage from $4.25 to $5.05. Pennsylvania didn't.
• 410 fast-food restaurants surveyed before (Feb–Mar) and after (Nov–Dec).
• Result: NJ employment rose by 2.33 full-time-equivalent workers per store relative to PA. Theory predicted a fall.
• Alternative: use each NJ store's "wage gap" (how much it had to raise wages). Coefficient 15.65 × average gap 0.11 ≈ +1.7 FTE.
• Prices of a meal rose about 3.3 % relative to PA. More full-time workers (+7.3 pp). No clear changes in opening hours.
• Debate: Neumark & Wascher (2000) used payroll data and found negative effects. Card & Krueger (2000) used administrative data and found none. The original paper showed no parallel-trends evidence, and one treated vs one control state limits inference.

How the causal methods fit together

One question, four methods: does schooling raise wages?

Why the numbers differ: different populations (everyone, compliers, people at a cut-off, treated cohorts) and different biases. If effects vary between people, these are different, legitimate numbers. State the estimand, check each design's assumptions, and treat agreement across methods as stronger evidence than any single estimate.

Which causal method?

1. Can you randomise? Run an experiment and compare means. Done.
2. Is there something random that pushes the treatment (lottery, weather, birth timing) but doesn't touch Y directly? Use IV.
3. Does a rule switch treatment on at a cut-off of some score, age or date? Use RDD (fuzzy RDD if the cut-off only changes the odds).
4. Did a policy hit some groups and not others, with data before and after? Use DiD (Callaway & Sant'Anna if timing is staggered).
5. None of these? Regression with controls, but be honest that it shows association unless you've controlled for everything that matters.

The three methods compared

Toolbox lectures in one line each

Log interpretation table

Standard errors: which ones?

• Error variance changes with x: heteroskedasticity-robust (HC) SEs.
• Treatment assigned to groups, or panel data: cluster at the level of treatment assignment.
• IV: use an IV command, never the manual second stage.
• RDD: robust bias-corrected intervals (rdrobust).
• Estimator with no simple SE formula, moderate n: bootstrap (not a cure for tiny samples).
• Weak first stage in IV: Anderson–Rubin (weak-instrument-robust) intervals.

How "mastered" works

• A lecture is mastered when you have answered at least 60 % of its questions in exam mode and got at least 80 % of those right (your latest exam answer to each question counts), or when you get at least 80 % of its questions right in the final test.
• Wrong answers go on a "missed" list. Each lecture header shows a Retry missed button, and the option above runs only those.
• After a week, mastered lectures show review due. A short mixed exam a few days later does more for memory than rereading.