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Econometrics
101

From Correlation to Credible Causation — a Foundational Course on Estimating Causal Effects for Development Practitioners in South Asia

Research-BackedSouth Asia Focus100 SlidesFree Access

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Agenda

What We Cover

What Econometrics Is

Slides 3–10

The Causal Question & the Counterfactual

Slides 11–19

OLS Regression, Properly Understood

Slides 20–28

Endogeneity & Omitted-Variable Bias

Slides 29–37

Randomised Experiments / RCTs

Slides 38–46

Instrumental Variables

Slides 47–55

Difference-in-Differences

Slides 56–64

Regression Discontinuity

Slides 65–73

Panel Data & Fixed Effects

Slides 74–82

Reading & Critiquing Results

Slides 83–92

Tools & Further Reading

Slides 93–99

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Section One

What Econometrics Is

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Definition

Econometrics, defined

Econometrics is where economics, statistics and real-world data meet. Its central ambition is not just to describe the world but to estimate causal effects — what would happen if we changed something.

Econometrics

The application of statistical methods to economic and social data in order to test theories and, above all, to measure the causal effect of a policy, programme or treatment on an outcome of interest.

You do not need heavy mathematics to think like an econometrician. You need to ask, relentlessly: compared to what?

Question type	Needs	Example
Descriptive	A representative sample	How many households are below the poverty line?
Predictive	Correlation and out-of-sample fit	Which households will fall below it next year?
Causal	A credible counterfactual	Did the transfer keep them above it?

Prediction and causation come apart completely. A model can forecast defaults perfectly using variables that cause nothing, and a causal estimate can predict badly — they answer different questions.

Most confusion in applied work comes from using a predictive model to answer a causal question. If your conclusion contains the word "should", you needed a design, not a fit.

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Three Ingredients

Economics + statistics + data

Economics

A theory of how people and markets behave — what to look for and why

Statistics

Tools to separate signal from noise and quantify uncertainty

Data

Surveys, censuses, admin records, experiments — the evidence itself

Take away any one ingredient and you get something less: theory without data is speculation; data without theory is pattern-hunting.

Ingredient	Supplies	Missing it means
Economic theory	Which variables matter and why	Data mining with no interpretation
Statistics	Uncertainty and inference	Point estimates with no error bars
Data	The evidence	A model nobody can test

Theory does the most under-appreciated work. It tells you which confounders are plausible, whether an exclusion restriction is credible, and whether an estimate should transfer — none of which the data can answer.

That is also why purely algorithmic approaches struggle with causal questions. Prediction can be learned from data; identification requires assumptions the data cannot supply.

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The Core Job

The question behind every study

Almost every econometric study is, at heart, answering one policy question: does X cause Y, and by how much?

Does a cash transfer raise school attendance?

→

Does a new road increase farm incomes?

→

Does microcredit lift consumption?

→

Does a midday meal cut child anaemia?

Each is a causal question. The whole discipline exists because answering it honestly is genuinely hard.

Policy question	The design its variation supports
Does a cash transfer raise attendance?	RCT, if roll-out can be randomised
Does a new road raise farm incomes?	DiD across phased construction
Does microcredit lift consumption?	RCT, or IV on branch placement rules
Does a scholarship raise completion?	RD at the score cutoff

The design is dictated by how the programme was implemented, not by preference. A phased roll-out gives you DiD; a score threshold gives you RD; neither can be conjured if the implementation had neither.

Which is why evaluators should be involved before implementation. A small change to the assignment rule — a lottery among equally eligible applicants — can convert an unevaluable programme into an evaluable one at almost no cost.

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The Trap

Correlation is not causation

Two things moving together — districts with more bank branches having higher incomes — does not mean one caused the other. The link could run the other way, or a third factor could drive both.

Whenever two variables are correlated, at least four explanations are possible — and only one of them is 'X causes Y'.

— a working principle of causal inference

Correlation between X and Y	Possible explanation
X causes Y	The claim being made
Y causes X	Reverse causality
Z causes both	Confounding
Selection into the sample	Collider bias — created by how you sampled
Chance	Especially with many comparisons

The fourth is the least known and the hardest to spot. Conditioning on something both X and Y affect — a common sample restriction — creates a correlation between them that does not exist in the population.

The discipline is to name all five explanations before defending the first. A study that only argues against confounding has answered one of four rival accounts.

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Why Naive Comparisons Fail

The comparison that fools you

Suppose villages with a microfinance branch have higher incomes than villages without one. Tempting conclusion: microfinance works. But branches were not placed at random — lenders chose more promising villages to begin with.

The income gap mixes the effect of microfinance with the pre-existing differences between the two kinds of village. Econometrics exists to pull these apart.

Why placement is not random	Direction of bias
Lenders choose promising villages	Overstates the effect
Programmes target the worst-off	Understates the effect
Villages with better roads get everything first	Overstates
Politically connected villages selected	Ambiguous, and correlated with much else

Programme placement is a decision, and decisions have reasons that also affect outcomes. The direction of the resulting bias depends entirely on the rule, which is why you must know how units were selected.

Ask the implementer directly how sites were chosen. It is the cheapest piece of research in any evaluation and it usually determines which designs are available to you.

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Description vs Causation

Two very different goals

Descriptive / predictive

Who is poor? Where is dropout highest? What will demand be next year? Correlations are enough here.

Causal

Will this programme reduce dropout? Here you must imagine a world without the programme — a counterfactual.

Most policy questions are causal. That is why this course spends most of its time on causal methods.

Task	Correlation enough?
Targeting: who is poor?	Yes
Forecasting demand next year	Yes
Deciding whether to fund a programme	No
Choosing between two designs	No
Describing where dropout is highest	Yes

Correlational work is not lesser work; it is different work. A well-built targeting model is enormously useful and answers no causal question, and problems arise only when it is read as one.

A quick test: does your sentence contain a hypothetical intervention? "If we did X, then Y" requires a counterfactual. "Where is Y highest" does not.

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The Credibility Revolution

How the field changed

From the 1990s onwards, econometrics shifted from elaborate models toward research designs that mimic experiments — the 'credibility revolution'. The 2019 and 2021 Nobel prizes recognised RCTs and natural-experiment methods used heavily in development.

2019

Nobel: Banerjee, Duflo & Kremer for the experimental approach to poverty

Sveriges Riksbank Prize

2021

Nobel: Card, Angrist & Imbens for natural experiments & causal methods

Sveriges Riksbank Prize

Before the credibility revolution	After
Elaborate structural models	Transparent research designs
Assumptions buried in functional form	One assumption, stated and debated
"Control for everything"	"Find exogenous variation"
Identification argued theoretically	Identification argued institutionally

The 2019 Nobel went to Banerjee, Duflo and Kremer for experimental approaches to poverty, and the 2021 prize to Card, Angrist and Imbens for natural experiments and causal methodology. Both recognised this shift.

The critique of the design-based approach is worth knowing too: it can favour questions that happen to have clean variation over questions that matter most, and LATE-type estimates over policy-relevant parameters.

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Section Two

The Causal Question & the Counterfactual

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The Big Idea

Compared to what?

A causal effect is always a comparison: the outcome with the treatment versus the outcome that would have occurred without it, for the very same unit, at the same time.

Counterfactual

What would have happened to a treated unit had it not been treated. It is never observed — which is the whole difficulty of causal inference.

Comparison	Valid counterfactual?
Treated units, before versus after	No — other things changed too
Treated versus untreated, same period	Only if they were comparable to begin with
Treated versus their own randomised control	Yes
Treated versus a matched comparison	Only on observables

Before-and-after is the most common evaluation in practice and the weakest. It attributes the entire trend — economic growth, other programmes, seasonality — to the intervention.

Matching is often presented as a design; it is adjustment with extra steps. It balances what you measured, which is precisely the confounding you were least worried about.

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Potential Outcomes

Two possible futures for each unit

The potential-outcomes framework imagines, for each person i, two outcomes:

Y₋(1)

outcome if person i receives the treatment

Y₋(0)

outcome if person i does NOT receive it

The individual causal effect is the difference Y₋(1) − Y₋(0). It is exactly what we want — and exactly what we can never see.

Notation	Meaning	Observed?
Y(1)	Outcome if treated	Only for the treated
Y(0)	Outcome if untreated	Only for the untreated
Y(1) − Y(0)	The individual causal effect	Never
E[Y(1)] − E[Y(0)]	The average treatment effect	Estimable, with a design

The framework’s value is that it makes the missing data explicit. Causal inference becomes a missing-data problem, and every design in this course is a strategy for filling in the blanks.

The framework carries an assumption usually left unstated — SUTVA: one unit’s treatment does not affect another’s outcome. Spillovers break it, and in village-level programmes they are common.

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The Core Obstacle

The fundamental problem of causal inference

For any one person we observe only one outcome: either the treated state or the untreated state, never both. The other is forever counterfactual.

The fundamental problem of causal inference: we can never observe both Y₋(1) and Y₋(0) for the same unit. Causal inference is, in essence, a missing-data problem.

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The Workaround

We estimate averages, not individuals

Since the individual effect is unknowable, we aim instead for the average treatment effect across a group — the mean of Y(1) minus the mean of Y(0) for a population.

Average Treatment Effect (ATE)

The average of the individual causal effects across all units in a population: what the treatment does on average, even though no single person's effect is observed.

The trick is finding a credible stand-in for the unobserved counterfactual outcome of the treated group.

Estimand	Answers
ATE	Effect if everyone were treated
ATT	Effect on those who actually were
ATU	Effect on those who were not
LATE	Effect on those an instrument moved

These differ whenever effects vary across people, which is almost always. Asking "what is the effect" is under-specified — the useful question is "the effect on whom".

For a scale-up decision you usually want the ATE or the ATU: the effect on people not yet reached. Most designs deliver the ATT or a LATE, which are effects on people already served.

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The Naive Estimate

Why a simple group difference goes wrong

We compare treated people's outcomes with untreated people's outcomes. But the untreated are different people — their average Y(0) need not equal the treated group's Y(0).

Observed gap = True effect (ATT) + Selection bias
Selection bias = how treated & untreated differ in Y(0) before any treatment

Component	What it is	Zero when
Observed gap	What you compute from the data	—
ATT	The true effect on the treated	The programme does nothing
Selection bias	E[Y(0)\|treated] − E[Y(0)\|untreated]	Groups are comparable in absence of treatment

Every design in this course is an argument that the last row is zero. RCTs make it zero by construction; the others argue it away with an assumption you have to evaluate.

Selection bias can exceed the true effect in size and go in either direction. That is why a naive comparison is not "approximately right" — it can have the wrong sign entirely.

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Selection Bias

The villain of the whole course

Selection bias

The systematic difference in (untreated) outcomes between those who get a treatment and those who do not, arising because they are not comparable to begin with.

Healthier people exercise more; richer farmers adopt new seeds first; motivated students attend coaching. Compare them with everyone else and you measure who they were, not what the treatment did.

Setting	Who selects in	Naive comparison suggests
Microfinance	Villages with better prospects	Microfinance works better than it does
Job training	The motivated and job-ready	Training works better than it does
Hospital use	The sick	Hospitals harm you
Fertiliser adoption	Richer farmers with better land	Fertiliser works better than it does

Three of four biases run the same way, which is why naive evaluations mostly overstate. Programmes tend to reach the already-advantaged, and their outcomes would have been better anyway.

The hospital row is the useful teaching case precisely because the answer is obvious. The identical logic is invisible when the topic is microcredit, and the bias is the same size.

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An Example

Do hospitals make people sicker?

People who visited a hospital last year report worse health than people who did not. Does the hospital harm them? Of course not — sick people go to hospital. The comparison is contaminated by who selects in.

This cartoon example is the same logic that wrecks naive evaluations of training, microcredit and health camps. Selection is everywhere.

Naive comparison	Selection story	True direction
Hospital users are less healthy	Sick people go to hospital	Hospitals help
Trained workers earn more	The employable enrol	Training helps less than shown
Insured people claim more	The unwell buy insurance	Adverse selection, not moral hazard alone

Each row is obvious once stated and invisible in a results table. The discipline is to ask, before reading any comparison, how people ended up on each side of it.

Write the selection story explicitly for your own evaluations. If you cannot articulate why the untreated are untreated, you cannot assess whether the comparison means anything.

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The Strategy

Every method is a counterfactual strategy

The rest of this course is a toolkit of research designs, each a different way to construct a credible counterfactual — a comparison group that plausibly shows what would have happened anyway.

RCTs: randomisation makes groups comparable

→

IV: an external nudge mimics random assignment

→

DiD: a comparison group tracks the trend

→

RD: units just above/below a cutoff are alike

Design	Source of the counterfactual	Load-bearing assumption
RCT	Randomly assigned control group	Randomisation worked and held
IV	Variation driven by the instrument	Exclusion restriction
DiD	Comparison group’s change over time	Parallel trends
RD	Units just the other side of a cutoff	No manipulation of the running variable
Fixed effects	The unit’s own past	No time-varying confounders

This table is the whole course. Each design buys a counterfactual with exactly one central assumption, and reading a paper means finding that assumption and asking whether it holds here.

None of these assumptions is testable directly. You can gather supporting evidence — balance tables, pre-trends, density tests — but the assumption itself is always an argument.

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Section Three

OLS Regression, Properly Understood

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The Workhorse

Regression: fitting a line through data

Ordinary Least Squares (OLS) finds the straight line that minimises the sum of squared vertical distances between the line and the data points. It is the workhorse of applied economics.

Y = α + βX + ε
outcome = intercept + slope × predictor + error

OLS does	It does not
Minimise squared vertical distances	Establish which variable causes which
Give the best linear fit to the data	Detect a non-linear relationship
Provide standard errors under assumptions	Validate those assumptions
Summarise an association	Deliver a counterfactual

Regression is a description tool that becomes a causal tool only when a design makes it one. The arithmetic is identical either way, which is exactly why the distinction has to be argued rather than computed.

Squared distances mean outliers pull the line hard. A handful of extreme observations can drive a coefficient, which is why influence diagnostics belong in every regression workflow.

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See It

A fitted regression line

Years of schooling vs monthly wage — OLS line of best fit

Illustrative

The slope says how much wage rises, on average, per extra year of schooling — in this data. Whether that slope is causal is a separate question entirely.

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What Regression Really Is

The conditional expectation function

Conditional Expectation Function (CEF)

E[Y | X] — the average value of the outcome Y for each value of the predictor X. OLS gives the best straight-line approximation to this function.

Read a regression as a machine that answers: for units with this value of X, what is the average Y? Nothing more is guaranteed.

Reading E[Y\|X]	Example
Average Y among units with this X	Mean wage among those with 10 years of schooling
OLS approximates it with a line	Best straight-line fit to those averages
A good approximation when	The true relation is roughly linear
A poor one when	The relation bends, or has thresholds

Reading regression as a conditional-average machine removes most of the mysticism. It answers "what is the average outcome for units that look like this" — no more, and that is a useful thing to know.

Plot the data before fitting. A scatter with a clear bend, or a cluster at zero, will be summarised by a straight line that describes neither region well.

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Reading a Coefficient

What a slope coefficient means

A coefficient β on X is the predicted change in Y associated with a one-unit increase in X, holding the other included variables fixed.

Two load-bearing words: 'associated' (not necessarily caused) and 'included' (only the variables you put in the model are held fixed — not the ones you left out).

Phrase in the coefficient’s meaning	What it hides
"Associated with"	Not necessarily caused by
"Holding other variables fixed"	Only the ones you included
"On average"	Effects may differ across the sample
"A one-unit increase"	Units matter; check whether X is logged

"Included" is the load-bearing word. A regression holds fixed the variables in the model and nothing else, so the coefficient describes a comparison across units that differ in every unmeasured way.

Read every coefficient aloud with "among the units in this sample, comparing those with the same measured characteristics". If the sentence then sounds like a weak claim, that is the claim.

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Multiple Regression

Controlling for other variables

Adding controls — Y = α + βX + γZ + ε — lets β describe the X–Y link among units with the same Z. This is how we try to compare like with like.

But you can only control for what you measure. The variables you cannot observe — ability, motivation, soil quality — are precisely the ones that cause trouble.

Adding a control	Effect
A genuine confounder you measured	Reduces bias — the intended case
A variable that causes Y but not X	Improves precision; no bias change
A mediator on the X→Y path	Removes part of the effect you wanted
A collider	Creates bias where there was none
A proxy for an unobservable	Reduces bias partly; residual remains

Two of the five make things worse, which is why "add more controls" is not a strategy. Whether a control helps depends on where the variable sits in the causal structure, not on whether it is available.

Controlling for a post-treatment variable is the commonest version of the third row, and it is easy to do by accident when the dataset was assembled after the programme ran.

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Units & Interpretation

Levels, logs and dummies

Form	Coefficient reads as	Common use
Y on X (levels)	ΔY in Y-units per 1-unit ΔX	Most variables
log Y on X	approx. % change in Y per 1-unit ΔX	Wages, income
log Y on log X	elasticity: % ΔY per 1% ΔX	Demand, output
Y on a dummy (0/1)	gap in mean Y between the two groups	Treated vs control

Knowing the functional form tells you how to translate a coefficient into a sentence a programme officer understands.

Specification	Coefficient reads as	Use
Y on X	ΔY in units per 1-unit ΔX	Most variables
log Y on X	Approximately % ΔY per unit ΔX	Wages, income
log Y on log X	Elasticity: % ΔY per 1% ΔX	Demand, output
Y on a 0/1 dummy	Difference in means between groups	Treatment indicators

The log-Y approximation degrades above roughly 0.1. For a coefficient of 0.5, the percentage change is about 65%, not 50% — use exp(β) − 1 when the coefficient is large.

Logs also drop zeros, which matters when the outcome is income or expenditure in a poor sample. Inverse hyperbolic sine is the usual workaround and has its own interpretation problems.

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When OLS Is Trustworthy

Gauss–Markov & BLUE

Under a set of assumptions — the Gauss–Markov conditions — OLS is BLUE: the Best Linear Unbiased Estimator. Among all linear unbiased methods, it has the smallest variance.

Best: lowest variance among linear unbiased estimators
Linear: it is a linear function of the data
Unbiased: on average it hits the true value
Estimator: a recipe for guessing the parameter

Gauss–Markov assumption	Fails when	Consequence
Linearity in parameters	The true relation is non-linear	Misspecification
Random sampling	The sample is selected	Biased and unrepresentative
No perfect collinearity	Two regressors move identically	Cannot estimate
Exogeneity	X correlates with the error	Biased — not causal
Homoskedasticity	Error variance varies with X	Wrong standard errors, not bias

Only one of these threatens causality. The last row affects inference and not the estimate, which is why robust standard errors solve it and nothing solves an exogeneity failure except a better design.

BLUE is a statement about efficiency within the class of linear unbiased estimators. It says nothing about whether the estimand is the causal effect — a distinction that trips up most first courses.

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The Crucial Caveat

Unbiased ≠ causal

The key Gauss–Markov assumption is that the error term is uncorrelated with X (exogeneity). If something in the error — an omitted cause — correlates with X, OLS is biased and the coefficient is not the causal effect.

This single assumption is where most of applied econometrics lives or dies. The next section is entirely about how it breaks.

Property	Guaranteed by Gauss–Markov?	What it means
Unbiased	Yes, given exogeneity	Right on average across samples
Efficient among linear estimators	Yes	Lowest variance in that class
Causal	No	Requires exogeneity to be true, not assumed
Correct standard errors	Only under homoskedasticity	Use robust errors otherwise

Unbiasedness is conditional on the assumption that fails most often. BLUE is a mathematical result about a model; whether that model describes your data is a separate empirical question.

This is the hinge of the whole course. Everything from here is about generating the exogeneity that Gauss–Markov assumes and observational data almost never supplies.

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Section Four

Endogeneity & Omitted-Variable Bias

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The Central Threat

Endogeneity, defined

Endogeneity

A situation where the explanatory variable X is correlated with the error term — that is, with something that also affects Y but is left out of the model. It makes the OLS coefficient biased and non-causal.

When X is exogenous, OLS recovers the causal effect. When X is endogenous, it does not. Diagnosing endogeneity is the practitioner's core skill.

Term	Means
Exogenous X	Uncorrelated with the error — OLS is causal
Endogenous X	Correlated with the error — OLS is biased
The error term	Everything affecting Y that is not in the model
Bias	The estimate is systematically wrong, not just noisy

Bias does not shrink with sample size. A biased estimate from a million observations is precisely wrong, and the tight confidence interval makes it more persuasive rather than less.

This is the single most important thing to carry out of the course: more data fixes noise, and only a better design fixes bias.

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Three Sources

Where endogeneity comes from

Omitted variables

A common cause of both X and Y is left out

Reverse causality

Y also affects X — the arrow runs both ways

Measurement error

X is recorded with noise, biasing its coefficient

All three break the exogeneity assumption. We take them one at a time.

Source	Mechanism	Typical fix
Omitted variables	A common cause of X and Y is missing	IV, RCT, fixed effects
Reverse causality	Y also affects X	IV, RD, timing
Measurement error in X	Noise attenuates the coefficient	Better data, or IV
Selection into the sample	Who is observed depends on Y	Model the selection

All four produce the same symptom — a biased coefficient — and require different remedies. Diagnosing which one you face is what determines the design, so it cannot be skipped.

They also co-occur. A study of microcredit faces placement selection, reverse causality and mismeasured income at once, which is why single-fix approaches rarely suffice.

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OVB

Omitted-variable bias, illustrated

Wage vs schooling — the same data split by (omitted) ability

Illustrative

Within each ability group the schooling slope is gentle. Pooled, a steep line appears — because higher-ability people get both more schooling and higher wages. OLS credits schooling for ability's effect.

OLS attributes to schooling	What is actually happening
The full pooled slope	Higher-ability people get more schooling and earn more anyway

The pooled line is steeper than any within-group line. That gap is the omitted-variable bias, visible in a picture in a way it never is in a coefficient table.

Ability bias in the returns to schooling is the classic case, and much of the IV literature — quarter of birth, distance to college, compulsory-schooling laws — exists to get around it.

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Sign of the Bias

Which way does OVB push?

The direction of omitted-variable bias depends on two signs: how the omitted variable Z relates to X, and how Z relates to Y.

Z → X	Z → Y	Bias on β
+	+	Upward (too big)
−	−	Upward (too big)
+	−	Downward (too small)
−	+	Downward (too small)

Even when you cannot fix OVB, you can often reason about its direction — and so bound how wrong your estimate might be.

Z→X	Z→Y	Bias on β
Positive	Positive	Upward — β too big
Negative	Negative	Upward
Positive	Negative	Downward
Negative	Positive	Downward

You can sign the bias without measuring the omitted variable. Ability plausibly raises both schooling and wages, so both signs are positive and the OLS return to schooling is biased upward.

That gives you a bound rather than an estimate, and a bound is often enough. If the biased estimate is already below the threshold that would justify a programme, the bias direction settles the decision.

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Reverse Causality

When the arrow runs both ways

Do more police cause more crime? Cross-section data often shows a positive correlation — because cities with more crime hire more police. Causation runs from Y to X.

More crime (Y)

→

leads cities to hire more police (X)

→

so X and Y correlate positively

→

even if police actually reduce crime

Sign of reverse causality	Check
The outcome plausibly drives the treatment	Ask which is decided first
Cross-sectional correlation with a puzzling sign	More police, more crime
Treatment responds to need	Programmes target the worst-off
Timing is unclear in the data	Look for a lag structure or a policy date

Reverse causality is why targeted programmes look ineffective in naive comparisons. Assistance flows to the struggling, so recipients do worse — and the programme takes the blame for the targeting.

Lagging the treatment variable is the common fix and rarely sufficient. If the assignment responded to an expected future outcome, a lag does not break the link.

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Measurement Error

Noise in X biases toward zero

When the predictor X is measured with random error — self-reported income, recalled expenditure — its coefficient is pulled toward zero. This is attenuation bias.

Counter-intuitive but important: messy measurement of X usually makes a real effect look smaller than it is, not larger. Noise in Y, by contrast, mainly inflates uncertainty.

Measurement error in	Effect
X (the regressor)	Attenuation — coefficient pulled toward zero
Y (the outcome)	Larger standard errors; no bias
A control variable	Incomplete control; residual confounding

Noise in X and noise in Y do completely different things, which is counter-intuitive and worth remembering: sloppy outcome measurement costs precision, sloppy treatment measurement costs the estimate.

Attenuation means self-reported income, recalled expenditure and mismeasured programme exposure all understate real effects — so a null result from noisy data is weak evidence of no effect.

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The False Comfort of Controls

More controls is not a cure

It is tempting to believe that adding enough control variables removes bias. But you can only control for what you observe and measure. Unobservables — motivation, ability, local governance — remain in the error.

Worse, controlling for the wrong variable — something caused by the treatment, or a collider — can introduce bias. Controls are a scalpel, not a sledgehammer.

Belief about controls	Reality
"More controls means less bias"	Only for genuine, well-measured confounders
"Controls fixed it — the coefficient barely moved"	It may not move for unobservables either
"A rich dataset means we controlled for everything"	Ability and motivation are in no dataset
"Adding controls is always safe"	Colliders and mediators create bias

The second row is the subtle one. Stability of a coefficient across control sets is often presented as robustness; it can equally mean your controls are uninformative about the confounding that matters.

The honest version of a controlled regression is: "this is the association among units similar on the variables we happened to measure." Everything beyond that is design, not adjustment.

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The Way Out

Design beats adjustment

Because we can never be sure we have controlled for every confounder, credible causal work relies on a research design that creates exogenous variation in X — variation unrelated to the unobservables.

The way to estimate a causal effect is not to control for everything, but to find variation in the treatment that is as good as random.

— the design-based view of econometrics

Approach	Relies on	Credible when
Adjustment (controls)	Having measured every confounder	Almost never, for behaviour
Design (RCT, IV, DiD, RD)	Exogenous variation in X	The assumption is defensible

This is the credibility revolution in one line. The field moved from modelling the confounders to finding variation that was never confounded in the first place.

It also explains why so much applied work now looks like detective work about institutions — roll-out dates, eligibility rules, arbitrary thresholds. Those are where exogenous variation actually comes from.

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Section Five

Randomised Experiments / RCTs

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The Gold Standard

Randomisation solves selection

In a randomised controlled trial (RCT), units are assigned to treatment or control by a coin flip. On average the two groups are identical in everything — observed and unobserved — except the treatment.

Because assignment is independent of potential outcomes, the control group is a credible counterfactual. Selection bias is designed away.

Randomisation delivers	Which no control set can
Balance on observables	A rich dataset can approximate this
Balance on unobservables	Nothing else does this
A known assignment mechanism	You do not have to guess how units selected in
A pre-specified analysis	Reduces scope for fishing

The second row is the entire argument for RCTs. Ability, motivation and local governance are balanced in expectation without anyone measuring them, which is what no regression can achieve.

Randomisation is a property of the assignment procedure, not of the resulting groups. A balance table is evidence the procedure worked; a chance imbalance in a small sample is possible and not a design failure.

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Why It Works

Balance in expectation

Randomisation does not make any two specific people identical. It makes the groups statistically equivalent, so their average Y(0) is the same. The control group's outcome stands in for the treated group's missing counterfactual.

Effect = mean Y(treated) − mean Y(control)
and with randomisation, selection bias ≈ 0

Randomisation makes	It does not make
Groups equivalent on average	Any two individuals identical
E[Y(0)] equal across arms	Every covariate exactly balanced
The control a valid counterfactual	The result generalise beyond the sample

Balance holds in expectation, which is a statement about the procedure rather than about your particular draw. Small samples can be imbalanced by chance and the design is still sound.

Stratified or block randomisation forces balance on key covariates while preserving the design. It is standard practice in field experiments with modest sample sizes.

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Check the Balance

A balance table

Baseline characteristics — treatment vs control (should be similar)

Illustrative balance check

Good randomisation produces near-identical groups at baseline. A balance table is the first thing to check in any RCT — it is the evidence that the design worked.

Reading a balance table	Concern
One variable differs at p < 0.05 out of 20	Expected by chance — not alarming
Several differ, all in one direction	Suggests the randomisation was compromised
Baseline outcome differs	Most serious — controls should be shown

Testing twenty variables at the 5% level produces one significant difference by construction. A single imbalance is not evidence against randomisation, and treating it as such is a misreading of the test.

What matters more is whether imbalance is systematic and whether it is on variables that predict the outcome. Those are the ones that would bias the estimate if unaddressed.

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J-PAL

RCTs in development: J-PAL & the field

The Abdul Latif Jameel Poverty Action Lab (J-PAL), founded in 2003, popularised RCTs in development. Hundreds of trials — many in India — have tested deworming, remedial teaching, immunisation incentives, and more.

A landmark example: Pratham's 'Teaching at the Right Level' remedial-education model was refined and scaled through a sequence of RCTs across Indian states.

Development RCT finding	Consequence
Remedial teaching by matched instruction	Pratham’s Teaching at the Right Level, scaled across states
Small incentives raise immunisation uptake	Camps plus lentils outperformed camps alone
Deworming and schooling	Contested after replication and re-analysis

The third row is the honest one to include. Trials produce contested findings as well as durable ones, and a course that presents only the successes teaches the wrong lesson about evidence.

J-PAL was founded in 2003 and its India work is extensive. The scaled examples matter most: an effect that survived transfer from trial to government delivery is a stronger result than the trial alone.

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Growth

The rise of development RCTs

Cumulative development RCTs registered (stylised, illustrative trend)

Illustrative — stylised to show the trend, not exact counts

The exact numbers here are illustrative, but the shape is real: development RCTs grew explosively after the mid-2000s.

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Two Kinds of Validity

Internal vs external validity

Internal validity

Is the estimated effect causally correct for this sample? RCTs are strong here — their headline virtue.

External validity

Will it hold elsewhere — other states, scales, populations? RCTs are often weak here.

A perfectly clean trial in one district may not generalise. 'It worked in Rajasthan' is not 'it will work in Bihar'.

	Internal validity	External validity
Question	Is the estimate right here?	Does it hold elsewhere?
RCTs	Strong by design	Often weak
Threatened by	Attrition, spillovers, non-compliance	Context, scale, population, implementer
Fixed by	Better design and execution	Replication and theory

A perfectly internally valid trial can be irrelevant to your decision. An intervention that worked in one district, delivered by a specialist NGO at pilot scale, tells you little about a state-wide government roll-out.

The general-equilibrium problem is the sharpest version: a job-training programme that helps its participants may simply reallocate scarce jobs, and a trial at pilot scale cannot detect that.

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Real-World Wrinkles

What can still go wrong

Threat	What happens	Fix / response
Attrition	Treated & control drop out differently	Track everyone; bound effects
Spillovers	Control units affected by treatment	Randomise at cluster level
Non-compliance	Assigned but don't take treatment	Analyse by assignment (ITT)
Hawthorne effects	Being watched changes behaviour	Blinding where possible

Intention-to-treat (ITT) — analysing people by the group they were assigned to — preserves the randomisation even when compliance is imperfect.

Threat	Symptom	Response
Attrition	Differential dropout between arms	Track everyone; report bounds
Spillovers	Control units affected by treatment	Randomise at cluster level
Non-compliance	Assigned but untreated, or vice versa	Report intention-to-treat
Hawthorne / John Henry	Behaviour changes from being observed	Blinding where possible

Intention-to-treat is the honest estimate under non-compliance. Comparing those who actually took up treatment reintroduces selection, undoing the randomisation entirely — a common and serious error.

Differential attrition is the threat that quietly destroys a trial. If the least successful participants drop out of the treatment arm, the surviving sample is no longer comparable to the control.

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Ethics

Is it ethical to randomise a benefit?

Randomise when there is genuine uncertainty about whether the programme works (equipoise)
Use waitlists or phased roll-outs so the control group eventually benefits
Never withhold a known, proven, life-saving treatment to run a trial
Secure informed consent and ethics-board (IRB) approval

Scarce budgets mean not everyone can be served at once anyway. A lottery for limited places can be both fair and a clean experiment.

Ethical condition	Meaning
Equipoise	Genuine uncertainty about whether it works
Scarcity	You could not have served everyone anyway
Informed consent	Participants know they are in a study
Ethics approval	Independent review, before fieldwork
Eventual access	Waitlist or phased roll-out

Scarcity is the strongest practical justification. Where a programme can reach only a third of eligible villages, a lottery is arguably fairer than the usual alternatives — proximity, connections or convenience.

Never randomise away a known effective, life-saving treatment. Equipoise is a factual condition about the state of evidence, not a formality to assert in an ethics application.

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Section Six

Instrumental Variables

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When You Can't Randomise

Borrowing randomness from nature

Often you cannot run an experiment — the treatment already happened, or randomising is impossible. An instrumental variable (IV) finds a source of variation in X that is 'as good as random'.

Instrumental variable (instrument)

A variable Z that shifts the treatment X but affects the outcome Y only through X. It isolates the part of X that is unrelated to the confounders.

You cannot randomise because	IV may still work if
The treatment already happened	Something as-good-as-random shifted it
Randomising is unethical	A natural source of variation exists
The programme is universal	Exposure varied by an arbitrary rule
Assignment was political	A separate quasi-random nudge exists

IV is what you reach for when the variation you need already exists somewhere in the world. The work is finding it and arguing that it is uncontaminated — not estimating anything difficult.

The estimation is mechanical; the credibility is entirely in the argument. This is why IV papers spend more space on institutional detail than on econometrics.

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The Logic

Use only the exogenous part of X

Instrument Z (as-good-as-random)

→

shifts treatment X

→

X changes the outcome Y

→

Z affects Y ONLY through X

IV throws away the endogenous, confounded variation in X and keeps only the clean variation driven by Z. That clean slice yields a causal estimate.

Stage	What is estimated	Diagnostic
First stage	Effect of Z on X	F-statistic — report it
Reduced form	Effect of Z on Y	If this is null, IV will be too
IV estimate	Reduced form divided by first stage	Sensitive to a weak denominator

Look at the reduced form first. If Z has no detectable effect on Y, no amount of scaling by the first stage will produce a credible effect — and a large IV estimate from a null reduced form is a warning sign.

IV is division, which is why a small first stage is dangerous: dividing by something near zero amplifies both noise and any small violation of the exclusion restriction.

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Two Conditions

An instrument must satisfy BOTH

1. Relevance

Z must actually shift X — a real, strong first-stage relationship between instrument and treatment. Testable in the data.

2. Exclusion restriction

Z must affect Y only through X — no other pathway, no direct effect, uncorrelated with the error. Untestable; argued, not proven.

BOTH are required. Relevance you can check; the exclusion restriction you must defend with theory and institutional knowledge — it is where most IV claims succeed or fail.

Condition	Testable?	How to argue it
Relevance — Z shifts X	Yes — first-stage F	Report the F-statistic
Exclusion — Z affects Y only via X	No	Institutional knowledge and argument
Independence — Z as good as random	Partly	Balance on covariates
Monotonicity — no defiers	No	Argument about behaviour

The one you cannot test is the one that matters most. Exclusion is defended by a story about the world, and evaluating that story is the whole job of reading an IV paper critically.

Ask what else Z could plausibly affect. Rainfall affects income — and also health, migration and school attendance, any of which could reach conflict without going through income.

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A Classic Example

Rainfall as an instrument

To study whether economic downturns fuel conflict, researchers have used rainfall shocks as an instrument for agricultural income in rain-fed economies. Rain is plausibly random year to year.

Relevance: rainfall strongly affects farm income (first stage)
Exclusion: rainfall is argued to affect outcomes only via income — the part you must defend
Caveat: if rain also affects, say, mobility or disease directly, exclusion fails

Rainfall as an instrument	Assessment
Relevance	Strong — rainfall drives rain-fed farm income
Independence	Plausible — annual weather is close to random
Exclusion	The weak link
Objections	Rain also affects health, migration, road access, mobilisation

Rainfall satisfies two conditions easily and the important one poorly. Any channel from weather to the outcome that bypasses income breaks the exclusion restriction, and there are several.

The lesson generalises: instruments that look wonderfully exogenous are often exogenous and multi-channel. Exogeneity is necessary and nowhere near sufficient.

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Another Example

Distance, sib-sex & quarter of birth

Instrument (Z)	Treatment (X)	Exclusion argument
Distance to a school/college	Years of schooling	Distance affects wages only via schooling
Quarter of birth	Years of schooling	Birth-month is arbitrary, tied to school-start laws
Sex composition of first 2 kids	Having a 3rd child	Sex mix is random, shifts fertility

Each is clever — and each has been challenged on exclusion grounds. A good IV invites scrutiny of the one assumption you cannot test.

Instrument	Exclusion argument	Standard objection
Rainfall	Weather affects income and nothing else relevant	Also affects health, migration, mood
Distance to school	Distance only matters via schooling	Families choose where to live
Quarter of birth	Birth month is arbitrary	Season of birth correlates with family type
Sibling sex composition	Sex of a first child is quasi-random	Not where sex selection occurs

Every classic instrument has a well-known objection, and the last is specific to South Asia. Sibling-sex instruments assume the sex of births is random, which sex-selective abortion violates directly.

The literature has moved towards more institutional instruments — policy rules, administrative thresholds, roll-out timing — precisely because their exclusion arguments are easier to make concrete.

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What IV Estimates

A local effect, for compliers

IV does not recover the average effect for everyone. It recovers the Local Average Treatment Effect (LATE) — the effect for the compliers, those whose treatment status is moved by the instrument.

So 'the IV estimate' answers a specific question: the effect on people the instrument actually nudged. Different instruments can give different — both correct — LATEs.

Group	Definition	Included in LATE?
Compliers	Treated because of Z	Yes — only these
Always-takers	Treated regardless of Z	No
Never-takers	Untreated regardless of Z	No
Defiers	Do the opposite of Z	Assumed not to exist

LATE is the effect on people you usually cannot identify. Compliers are defined by a counterfactual response, so you can characterise them statistically but never list them.

This matters for policy. If your instrument is distance to school, the compliers are people near the margin of attending — and a policy aimed at everyone will not have this effect.

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Weak Instruments

The danger of a weak first stage

If Z only weakly predicts X (a weak instrument), IV estimates become wildly imprecise and can be more biased than plain OLS — even tiny exclusion violations get amplified.

Rule of thumb: report the first-stage F-statistic; a common (rough) threshold is F > 10. A weak instrument is worse than no instrument at all.

First-stage F	Interpretation
Below 10	Weak instrument — treat results with suspicion
Around 10	The traditional rule of thumb, now considered too lenient
Well above 10	Adequate relevance
Not reported	Ask why

The F > 10 rule is a rough convention and recent work argues it is too permissive. Weak-instrument-robust inference exists and should be used when the first stage is anywhere near the boundary.

With a weak instrument, IV can be more biased than plain OLS, and biased toward the OLS estimate — so a weak-IV result that "confirms" OLS is confirming nothing.

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Reading IV Critically

Three questions for any IV study

Is it relevant? Is the first stage strong (high F)?
Is exclusion plausible? What is the story for 'only through X', and what would break it?
Whose effect is it? Who are the compliers — and do you care about them?

A persuasive IV paper spends most of its words defending the exclusion restriction, not running the regression.

Question	Where the answer lives
Is it relevant?	The first-stage F, reported in the table
Is exclusion plausible?	The institutional argument in the text
Whose effect is this?	The complier characterisation, often absent
Does the reduced form hold?	Z on Y directly — ask for it

A persuasive IV paper spends most of its length on the second row. If the exclusion argument occupies one sentence, the authors have not done the work that makes the estimate credible.

Complier characterisation is increasingly expected and still often missing. Without it you have an effect on an unnamed subpopulation, which is hard to apply to any policy decision.

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Section Seven

Difference-in-Differences

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The Idea

Before-and-after, with a comparison group

Difference-in-Differences (DiD) studies a policy that hits one group but not another. It compares the change in the treated group with the change in an untreated comparison group.

Difference-in-Differences

An estimator that subtracts the before–after change in a comparison group from the before–after change in the treated group, netting out both fixed group differences and common time trends.

	Before	After	Difference
Treated group	A	B	B − A
Comparison group	C	D	D − C
DiD estimate	—	—	(B − A) − (D − C)

The first difference removes anything fixed about each group; the second removes anything that changed for both. What survives is what changed for the treated and not the comparison.

DiD requires only repeated cross-sections, not a panel of the same units — which is why it works with survey rounds where individuals cannot be linked over time.

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The Two Differences

Why subtract twice?

Difference 1

Treated group: after − before (removes fixed traits of the group)

Difference 2

Comparison group: after − before (captures what would have happened anyway)

The DiD estimate is Difference 1 − Difference 2. The comparison group's change is the counterfactual trend for the treated group.

Difference removes	Which handles
First: treated after minus before	Everything fixed about the treated group
Second: comparison after minus before	Everything that changed for both groups
What remains	What changed only for the treated

The second difference is the comparison group doing its job: it measures the common trend — growth, seasonality, national policy — that a before-and-after study would have credited to the programme.

This also shows what DiD cannot remove: anything that changed for the treated group alone, for reasons unrelated to the treatment. That is precisely the parallel-trends assumption.

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See It

A difference-in-differences plot

Outcome over time — treated vs comparison, policy at 'After'

Illustrative

The DiD effect is the gap between the treated group's actual outcome (58) and its counterfactual (46) — about 12 points. The dashed red line is the assumed parallel trend.

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The Key Assumption

Parallel trends — not equal levels

DiD is valid only if, absent the policy, the two groups would have moved in parallel — the same trend over time. The groups need NOT start at the same level.

Common error: thinking DiD requires the groups to be identical before treatment. It does not. It requires their trends to be parallel — a statement about slopes, not levels.

Requirement	DiD needs it?
Equal levels before treatment	No — the commonest misunderstanding
Parallel trends absent treatment	Yes — the whole assumption
Similar groups	Helpful, not required
The same units observed twice	No — repeated cross-sections work

Levels can differ by any amount; it is the trajectories that must match. A comparison group at half the treated group’s baseline is fine if both were rising at the same rate.

Parallel trends is a counterfactual claim about a period that did not happen, so it can never be tested directly. Pre-trend evidence supports it; it does not establish it.

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Defending It

How to support parallel trends

Plot pre-treatment trends: did the groups move together before the policy?
Run a placebo / event-study check on pre-periods
Choose a comparison group as similar as possible to the treated one
Be honest: parallel trends is an assumption, never fully provable

Parallel pre-trends do not prove parallel counterfactual trends — but their absence is a serious warning sign.

Evidence for parallel trends	Strength
Plot several pre-treatment periods	The minimum expected
Event-study coefficients, pre-period near zero	Stronger
Placebo test on a fake earlier treatment date	Strong
A comparison group chosen for similarity	Supportive, not evidence
One pre-period only	Almost none

A single pre-period cannot show a trend. Two points determine a line, and the assumption is about the line — so a paper with one pre-period has offered no evidence at all.

Parallel pre-trends make the assumption more plausible without proving it. A policy anticipated in advance can produce flat pre-trends and violated parallel trends simultaneously.

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Natural Experiments

When policy creates the design

DiD shines with natural experiments — policies rolled out to some states/districts and not others, or at different times. The staggered roll-out supplies the treatment and comparison groups.

Indian examples: the phased district roll-out of NREGA (2006–08), or state-level reforms introduced in some states before others, are natural settings for DiD.

Natural experiment	Why it works
Phased district roll-out	Later districts serve as comparisons for earlier ones
A policy in some states only	Neighbouring states as comparison
An eligibility rule change	Cohorts either side of the change
An unanticipated shock	Nobody could adjust in advance

The last row is the strongest and rarest. Anticipation is the main threat to the others: if districts knew they were next, behaviour shifts before the official date and contaminates the pre-period.

Ask how roll-out order was decided. If the earliest districts were chosen for readiness or political importance, the comparison groups differ systematically and parallel trends is doubtful.

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When It Breaks

Threats to a DiD design

Threat	What it does	Watch for
Diverging trends	Groups were drifting apart anyway	Non-parallel pre-trends
Other shocks	A second event hits only one group	Concurrent policies
Composition change	Who is in each group shifts over time	Migration, attrition
Anticipation	Behaviour changes before the policy	Pre-period jumps

Recent methods literature also warns that staggered roll-outs with two-way fixed effects can mislead if effects vary over time — use modern DiD estimators.

Threat	What to look for
Diverging pre-trends	The event-study plot before treatment
A concurrent shock	What else happened to one group at that time?
Composition change	Migration, attrition, sample redefinition
Anticipation	Behaviour shifting before the official date
Staggered adoption	Whether a modern estimator was used

The last row is a live methodological issue. With treatment timing that varies across units, the standard two-way fixed-effects estimator can produce a weighted average with negative weights and the wrong sign.

Estimators from Callaway and Sant’Anna, Sun and Abraham, and Borusyak and co-authors address this. A staggered DiD published without one of them, or an equivalent, warrants scepticism.

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Reading DiD Critically

Questions for any DiD study

Did the authors show parallel pre-trends?
Is the comparison group genuinely comparable?
Could another shock have hit only one group at the same time?
With staggered timing, did they use an appropriate modern estimator?

DiD is powerful and intuitive — which is exactly why its one assumption deserves the hardest scrutiny.

Question for a DiD paper	Red flag if
Are pre-trends shown?	Only one pre-period
Is the comparison group defensible?	Chosen with no stated rationale
Any concurrent shock?	Not discussed
Staggered timing handled?	Plain two-way fixed effects
Standard errors clustered?	At the wrong level, or not at all

Two of these five are recent additions to the checklist. Staggered-adoption problems and clustering practice have both changed materially, so older papers can be sound work by the standards of their time and still need re-examination.

DiD is powerful and heavily used, which makes it heavily misused. It is the design where a plausible-looking result most often rests on an assumption nobody checked.

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Section Eight

Regression Discontinuity

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The Idea

Assignment by an arbitrary cutoff

Many programmes use a threshold rule: a scholarship for scores above 60, a poverty scheme for those below a deprivation score. Regression Discontinuity (RD) exploits that sharp cutoff.

Regression Discontinuity (RD)

A design that compares units just above and just below a cutoff on a 'running variable'. Near the threshold, who lands on which side is essentially random, so the two sides are comparable.

RD needs	Check
A cutoff rule that determines eligibility	Is it actually enforced?
A continuous running variable	Not a category dressed as a score
Enough observations near the cutoff	Bandwidth versus precision
No precise manipulation	Density test around the threshold

Eligibility rules are everywhere in South Asian programmes — BPL lines, SECC deprivation scores, exam cutoffs, population thresholds triggering a facility — which makes RD unusually available here.

The rule must actually bind. Where local officials routinely override the cutoff, you have a fuzzy design at best and no design at all if the overrides correlate with the outcome.

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Why It Works

Just-above ≈ just-below

A student scoring 59 and one scoring 61 are, in every meaningful way, alike — ability, background, motivation. Yet one gets the programme and the other does not. The cutoff manufactures a local experiment.

The jump in the outcome at the threshold — a discontinuity that nothing else can explain — is the causal effect of the programme.

Why 59 and 61 are comparable	Why 40 and 80 are not
A two-point gap is mostly noise	A forty-point gap is real ability
Neither could control which side they landed	They differ systematically
Backgrounds are similar in expectation	Backgrounds differ

The cutoff manufactures a local experiment out of an administrative decision. Nobody randomised anything; the arbitrariness of the threshold does the same work over a narrow window.

That local quality is both the strength and the limit. The comparison is airtight near the cutoff and says nothing about anyone far from it, which is a real constraint on policy use.

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See It

A jump at the cutoff

Outcome vs running variable — treatment assigned above the cutoff (50)

Illustrative

The vertical jump at the cutoff (50) — roughly 41 to 53 — is the estimated effect. The smooth slope on each side is the relationship that would hold without any jump.

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Sharp vs Fuzzy

Two flavours of RD

Sharp RD

Crossing the cutoff perfectly determines treatment — everyone above is treated, everyone below is not.

Fuzzy RD

Crossing the cutoff only raises the probability of treatment. The jump in take-up is used like an instrument.

Fuzzy RD is essentially IV at the threshold: the cutoff instruments for actual treatment.

	Sharp RD	Fuzzy RD
Crossing the cutoff	Determines treatment	Raises its probability
Estimate	Jump in the outcome	Jump in outcome / jump in take-up
Equivalent to	—	IV, with the cutoff as instrument
Interpretation	Effect at the cutoff	LATE for compliers at the cutoff

Fuzzy RD inherits every IV caveat. It is division again, so a small jump in take-up at the threshold produces an unstable estimate for the same reason a weak instrument does.

Most real programmes are fuzzy: some eligible households never enrol and some ineligible ones do. Treating a fuzzy design as sharp overstates take-up and understates the effect.

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Local Validity

RD gives a LOCAL effect

RD estimates the effect only at the cutoff — for units near the threshold. It says little about people far from it.

Key caveat: the RD effect is local. A scholarship's effect for students scoring 59–61 may differ entirely from its effect for those scoring 90. Do not over-generalise the jump.

RD estimates the effect	It does not estimate
At the cutoff	The effect far from the cutoff
For marginal units	The effect for clearly eligible units
Under the current rule	What would happen if the cutoff moved

The third row is the policy-relevant limitation. An RD tells you the effect at a threshold and not what happens if you shift the threshold — which is usually the decision being contemplated.

The local effect can still be exactly what is needed. Whether to extend a scholarship to those just below the line is precisely a question about marginal students.

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The Main Threat

Manipulation of the running variable

RD fails if people can precisely manipulate which side of the cutoff they land on — an examiner nudging a 59 to a 61, a household mis-reporting assets to qualify.

Diagnostic: check for bunching — a suspicious pile-up of cases just on the favourable side of the cutoff (a McCrary density test). Smoothness across the threshold is the credibility test.

Manipulation evidence	Diagnostic
Bunching just above the cutoff	McCrary density test
Covariates jump at the threshold	They should be smooth
Suspicious rounding in scores	Look at the raw distribution
Discretion in who is assessed	Institutional knowledge

Manipulation is the one threat that destroys RD outright. If people can position themselves precisely, those just above the cutoff differ from those just below in exactly the ways that matter.

Partial manipulation is common and less fatal: examiners nudging borderline scores upward affects a narrow band, and a donut RD excluding the immediate neighbourhood of the cutoff is the standard response.

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Practical Choices

Bandwidth and functional form

Bandwidth: how wide a window around the cutoff to use — narrow is cleaner but noisier
Functional form: fit flexible curves each side; beware high-order polynomials that invent jumps
Covariate smoothness: other variables should NOT jump at the cutoff — a useful placebo check

Good RD work shows the estimate is robust to the bandwidth choice, not an artefact of one window.

Choice	Trade-off	Good practice
Bandwidth	Narrow is cleaner but noisier	Show results across bandwidths
Functional form	Flexibility versus invented jumps	Local linear; avoid high-order polynomials
Covariates	Should not change the estimate much	Report with and without
Placebo cutoffs	Should find nothing	Test several

High-order global polynomials manufacture discontinuities that are not there — a well-documented failure. Local linear estimation with a data-driven bandwidth is the current standard.

A result that appears only at one bandwidth is not a result. The sensitivity plot across bandwidths is the single most informative figure in an RD paper.

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Where RD Fits

RD in development practice

RD is ideal wherever eligibility hinges on a score or threshold: poverty-line targeting (BPL cutoffs, SECC deprivation scores), exam-based scholarships, population thresholds that trigger a facility or grant.

Because eligibility rules are everywhere in Indian welfare programmes, RD is often the most natural — and most credible — design available to an evaluator.

Indian eligibility rule	RD opportunity
BPL and SECC deprivation scores	Households just either side of the cutoff
Exam-based scholarships	Students just above and below the mark
Population thresholds for a facility	Villages just either side
Land-holding ceilings for schemes	Farms just either side

Threshold rules are pervasive in Indian programme design, which makes RD unusually available here. Any scheme with a score-based eligibility test is a potential design waiting for someone to use it.

Check enforcement before assuming a design exists. Where local discretion routinely overrides the score, you have fuzzy assignment at best and manipulation at worst.

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Section Nine

Panel Data & Fixed Effects

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Following Units Over Time

What panel data buys you

Panel data tracks the same units — households, districts, firms — across multiple periods. This repeated observation lets us net out stable, unchanging differences between units.

Panel (longitudinal) data

Data on the same set of units observed at two or more points in time, combining a cross-section with a time dimension.

Panel data allows	Cross-section does not
Netting out fixed unit characteristics	Cannot — they are unobserved
Observing change within a unit	Only differences between units
Controlling for common time shocks	No time dimension
Studying dynamics and lags	No

Repeated observation is what converts unobservable characteristics into something you can remove. You never learn what they are; you simply arrange the comparison so they cancel.

The cost is attrition. Panels lose units over time and the losses are rarely random, which reintroduces exactly the selection the design was meant to eliminate.

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The Core Trick

Each unit becomes its own control

With fixed effects, we compare each unit to itself over time. Anything about the unit that stays constant — and so cannot explain changes — is swept out of the comparison.

Yᵢₜ = βXᵢₜ + αᵢ + δₜ + εᵢₜ
αᵢ = unit fixed effect  δₜ = time fixed effect

Fixed effect	Absorbs
Unit (αᵢ)	Everything constant about that unit — geography, culture, institutions
Time (δₜ)	Everything affecting all units in that period — national shocks, inflation
Both	The standard two-way specification
Unit-specific trends	Different trajectories per unit — demanding of the data

Unit fixed effects control for unmeasured characteristics you never had to name, which is their power. They cost you any variable that does not change within a unit — you cannot estimate the effect of caste or geography.

Adding unit-specific trends is often proposed as a robustness check. It is a strong requirement and frequently leaves too little variation to identify anything.

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The Within Estimator

Fixed effects use within-unit variation

The fixed-effects (or within) estimator subtracts each unit's own average from every observation, so β is identified only from how a unit changes relative to itself over time.

Differences between units — rich vs poor district, fertile vs arid land — are discarded. Only the within-unit story remains, and that is what removes time-invariant confounders.

Within estimator uses	Discards
How a unit changes over time	Differences between units
Units that actually change	Units with no variation — they contribute nothing
Variation after de-meaning	Any time-invariant regressor

Units that never change drop out of the estimation entirely. If only a handful of districts switched treatment status, your result rests on those few, whatever the total sample size suggests.

Report how much identifying variation there is: how many units switched, when, and in which direction. A fixed-effects estimate on n = 50,000 driven by three districts is a different claim.

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The Crucial Limit

Fixed effects remove only TIME-INVARIANT confounders

Unit fixed effects control for everything about a unit that is constant over time — geography, culture, fixed institutions — even if you never measured it.

Critical caveat: they do nothing about confounders that change over time. A district-specific shock that moves with the treatment will still bias β. Fixed effects are not a magic exogeneity machine.

Confounder	Fixed effects handle it?
District geography and climate	Yes — time-invariant
Persistent local institutions	Yes
A district-level policy change	No — time-varying
Local economic growth	No
Changing local leadership	No

Fixed effects are frequently over-sold as solving confounding. They solve exactly one class of it, and the confounders that most often drive results in development — other things happening at the same time — are not in that class.

Ask what else changed in treated units during the study window. If a state adopted three reforms in the same year, unit fixed effects separate none of them.

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Fixed vs Random Effects

Two ways to model the unit term

	Fixed effects	Random effects
Assumes	Unit term may correlate with X	Unit term uncorrelated with X
Uses	Within-unit variation only	Within + between variation
Robust to	Time-invariant confounding	More efficient if assumption holds
Safer when	You fear omitted unit traits	Strong, often unrealistic

For causal work where you worry about unobserved unit traits, fixed effects is usually the safer default — it makes the weaker assumption.

	Fixed effects	Random effects
Assumes	Unit term may correlate with X	It does not
Uses	Within-unit variation only	Within and between
Efficiency	Lower	Higher, if the assumption holds
Robustness	Robust to time-invariant confounding	Biased if the assumption fails

Default to fixed effects in applied causal work. The random-effects assumption — that unobserved unit characteristics are uncorrelated with the treatment — is exactly what you doubted in the first place.

A Hausman test compares the two. Failing it means random effects are inconsistent; passing it is weak evidence, since the test has low power in the samples typical of development data.

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First Differences

A close cousin: differencing

With two periods, first-differencing — regressing the change in Y on the change in X — removes the fixed unit term just as fixed effects do. (DiD is exactly this idea with a comparison group.)

Fixed effects, first differences and DiD are a family: all exploit repeated observation to subtract away stable, unobserved differences between units.

Estimator	Relationship
First differences	Removes the unit term by subtracting last period
Fixed effects	Removes it by subtracting the unit mean
DiD	First differences, with a comparison group
With two periods	First differences and fixed effects are identical

These are one family, not four methods. Each removes a unit-specific term by differencing something away, and they differ mainly in what they subtract and how many periods they use.

With more than two periods they diverge, and which is preferable depends on the error structure — first differences handle serially correlated errors better, fixed effects are more efficient otherwise.

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Standard Errors

Why you must cluster

In panel data, a unit's observations are correlated across time — this year looks like last year. Ignoring that makes standard errors far too small and 'significance' spurious.

Fix: cluster the standard errors at the unit level (e.g. by district or village). Clustering acknowledges that observations within a group are not independent — honest uncertainty, not inflated confidence.

Cluster at	When
The unit of treatment assignment	Almost always the right answer
Village or district	When treatment varies at that level
Too fine a level	Standard errors too small; false significance
Too few clusters (under ~40)	Cluster-robust errors themselves unreliable

Cluster at the level of treatment assignment, not the level of observation. A village-randomised programme analysed with household-level standard errors will report significance that is not there.

With few clusters the correction fails in the other direction. Wild cluster bootstrap is the standard remedy, and a paper with twelve clusters and conventional standard errors is reporting fiction.

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Reading Panel Work

Questions for a fixed-effects study

Are both unit and time fixed effects included where needed?
Could a time-varying confounder still drive the result?
Are standard errors clustered at the right level?
Is β identified from credible within-unit variation, or a few odd cases?

Fixed effects buy a lot — but remember what they cannot buy: protection from confounders that move over time.

Question	Weak answer
Are unit and time effects both included?	Only one, with no reason given
Could a time-varying confounder drive this?	Not discussed
Are errors clustered correctly?	At the observation level
Where does the variation come from?	Unreported

The second question is the one fixed-effects papers most often dodge. Absorbing time-invariant confounders is presented as if it addressed confounding in general, and it does not.

Ask what else changed in treated units during the window. In development settings, programmes arrive in bundles, and fixed effects separate none of them from one another.

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Section Ten

Reading & Critiquing Results

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Uncertainty

Standard errors quantify sampling noise

Standard error

A measure of how much an estimate would vary across repeated random samples. It quantifies sampling uncertainty — how precisely the effect is pinned down — not whether the design is valid.

A small standard error says the number is precise. It says nothing about whether the number is right — a biased design gives precisely wrong answers.

A small standard error means	It does not mean
The estimate is precisely measured	The estimate is correct
Sampling noise is low	The design is valid
A large sample, or low variance	The absence of bias

Precision and validity are independent. A biased estimate from administrative data covering a whole population has essentially no sampling error and is still wrong.

This is why design questions come first when reading a paper. If the identification fails, the standard errors describe how precisely you have measured the wrong quantity.

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Confidence Intervals

Report a range, not just a point

A coefficient of 0.12 is shorthand. The honest version is a confidence interval — say [0.04, 0.20] — the range of effects consistent with the data at, usually, 95% confidence.

If a 95% interval comfortably includes zero, the data cannot rule out 'no effect'. Always read the interval, not just the point estimate or the stars.

Reported as	Tells you
β = 0.12	A point estimate and nothing else
β = 0.12 (se 0.04)	Precision; you can compute the interval
β = 0.12, 95% CI [0.04, 0.20]	The range consistent with the data
β = 0.12***	Only that it differs from zero

Stars are the least informative way to report a result and the most common. They tell you about a comparison with zero, which is rarely the comparison a decision-maker needs.

An interval that includes zero does not mean no effect. It means the data cannot distinguish the effect from zero — which with a small sample is entirely compatible with a large true effect.

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See It

Same point estimate, very different certainty

Three studies, all estimating a +4-point effect (95% intervals)

Illustrative

All three centre on +4, but only Study A rules out zero. Study C's interval spans negative values — its 'effect' is indistinguishable from no effect. The point estimate alone hides this.

Study	Estimate	Interval	Conclusion
A	+4	[+2, +6]	Effect, precisely estimated
B	+4	[0, +8]	Suggestive; cannot rule out zero
C	+4	[−6, +14]	Uninformative

All three would be reported as "an effect of 4 points". Only the interval distinguishes a finding from noise, which is why point estimates quoted alone are close to meaningless.

Study C is also compatible with a large positive effect. A wide interval is not evidence of no effect — it is evidence that the study could not tell.

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Significance

What a p-value does — and doesn't — say

p-value

The probability of seeing an estimate at least this extreme if the true effect were zero. A small p-value means the result is unlikely under 'no effect' — nothing more.

Statistically significant ≠ large, important, or causally valid. With a big sample a trivial effect can be 'significant'. Always ask: how big is the effect, and from a credible design?

A p-value is	A p-value is not
P(data this extreme \| no effect)	P(no effect \| data)
A statement about sampling	A statement about importance
Dependent on sample size	A measure of effect size
Meaningful only if the design is valid	A substitute for identification

The first row is the error almost everyone makes. A p-value of 0.03 does not mean a 3% chance the effect is zero — that is a different quantity requiring a prior.

With a large enough sample, a trivially small effect becomes significant. With a small one, an important effect may not be. Significance is a statement about precision, not about the world.

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Effect Size

Is the effect big enough to matter?

An effect can be real, precise and significant — yet too small to justify the cost. Always translate a coefficient into something a decision-maker feels: rupees, percentage points, children, school days.

Pair statistical significance with practical significance and a cost comparison. 'Significant' is the start of the conversation, not the end.

Coefficient	Translated
0.12 log points on wages	About 12% higher earnings
0.08 standard deviations on test scores	A few weeks of additional learning
2.3 percentage points on enrolment	23 additional children per 1,000
₹340 per household per year	Compare against the cost per household

Standard-deviation effects are the least interpretable and the most reported in education research. Always ask what they translate to in learning time, or you cannot judge whether the programme is worth its cost.

Pair every effect with its cost per unit. An intervention with a small but very cheap effect can beat a large expensive one, and neither statistic answers that alone.

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Robustness

Does the result survive poking?

Does the estimate hold across alternative specifications and control sets?
Does it survive different samples, sub-groups and outlier handling?
Are there placebo tests that should find nothing — and do?
Do the authors show the result is not knife-edge on one choice?

A finding that appears only under one precise specification is fragile. Credible results are robust ones.

Robustness check	What it would reveal
Alternative specifications	Whether the result depends on modelling choices
Alternative samples	Whether it is driven by a subgroup
Outlier handling	Whether a few observations carry it
Placebo tests	Whether the design finds effects where none should exist
Multiple-hypothesis correction	Whether it survives testing many outcomes

Placebo tests are the most informative and the least performed. A design that detects an effect on an outcome the programme could not possibly affect has failed, whatever it reports elsewhere.

Beware the robustness section that shows twelve variants all significant at exactly 5%. Genuine robustness looks like a coefficient that moves a little; identical results across variants suggests selection.

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p-hacking

The garden of forking paths

Try enough specifications, subgroups and outcomes and some will cross p < 0.05 by chance. Reporting only those — p-hacking — manufactures false findings that will not replicate.

Be wary of a lone 'significant' subgroup, an oddly specific specification, or many outcomes with one star. Ask what was tested but not reported.

Forking path	How it inflates false findings
Many outcomes tested, one reported	One in twenty crosses 0.05 by chance
Subgroup analysis after seeing results	Subgroups multiply the comparisons
Specification chosen after the fact	Selection on the result
Outliers dropped once the answer is known	Selection again

None of this requires dishonesty. A researcher making each choice in good faith, informed by the data, produces the same inflation as one fishing deliberately — which is why pre-registration exists.

Be most suspicious of a single significant subgroup with no prior reason to expect it. That is the signature pattern, and such findings replicate poorly.

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Pre-registration

Tie your hands in advance

A pre-analysis plan — specifying hypotheses, outcomes and methods before seeing the data — removes the freedom to fish. Registries (e.g. the AEA RCT Registry) make the commitment public.

Pre-registration cannot make a bad design good, but it makes an honest design credible — readers know the result was not cherry-picked after the fact.

A pre-analysis plan fixes	Before
Primary and secondary outcomes	Data collection
The main specification	Seeing results
Subgroups to be examined	Any subgroup analysis
Multiple-testing correction	Reporting

Pre-registration cannot rescue a bad design. It makes deviations visible, which is a different and more limited claim than the one often made for it — and still a substantial improvement.

Read the registered plan against the published paper. Outcomes that appear in one and not the other, or a primary outcome demoted to secondary, is the check the registry exists to enable.

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External Validity

Will it travel?

A clean estimate is internally valid for its setting. Whether it generalises — to another state, scale, time or population — is external validity, a separate and often harder question.

Ask: what was the context and the sample? Would the mechanism plausibly work elsewhere? Scaling up can itself change the effect (general-equilibrium and implementation effects).

Before transferring an estimate, ask	Because
Who was in the sample?	The effect may be specific to them
What was the context?	Complementary conditions may be absent
Who implemented it?	A specialist NGO is not a line department
At what scale?	General-equilibrium effects appear at scale
What was the counterfactual?	The control condition differs across settings

The last row is the most neglected. A programme evaluated against nothing looks better than the same programme evaluated against an existing service — and the comparison, not the programme, differs.

Theory is what makes transfer possible. If you understand the mechanism, you can predict where it will and will not hold; without one, you are extrapolating a number.

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Section Eleven

Tools & Further Reading

To go further, you need	Start with
Intuition before mathematics	Angrist & Pischke, Mastering ‘Metrics
The design-based reference	Mostly Harmless Econometrics
Code alongside theory	Cunningham, Causal Inference: The Mixtape, free online
Development applications	J-PAL and IPA policy briefs

Start with Mastering ‘Metrics if you have no econometrics background. It covers the same five designs with minimal mathematics and is the gentlest credible entry point.

The Mixtape is free and includes runnable code in both R and Stata, which makes it the fastest route from reading about a design to estimating one.

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Software

What practitioners actually use

Tool	Good for	Note
Stata	Applied micro-econometrics, panel, IV, RD	Industry standard; paid
R	Free, flexible, reproducible analysis & graphics	Rich causal-inference packages
Python (statsmodels, linearmodels)	Automation, large data, ML	Free, general-purpose
Excel / Sheets	Quick description, not inference	Fine to start; outgrow it

The software matters far less than the research design. A clean design in Excel beats a flawed one in Stata.

Tool	Strength	Consideration
Stata	The applied-micro standard; panel, IV, RD packages	Paid licence
R	Free; strong causal-inference ecosystem	Steeper start
Python	Automation, large data, integration	Fewer specialised econometrics packages

Choose by what your collaborators use. Reproducibility across a team matters more than any feature difference, and code nobody else can run is a liability in a multi-year project.

Whichever you pick, keep the analysis as a script rather than a sequence of clicks. Every design in this course requires showing your working, and a script is what makes that possible.

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Method Cheat-Sheet

Which design for which situation?

If you can…	Use	Key assumption
Randomise treatment	RCT	Successful randomisation
Find an as-good-as-random nudge	IV	Relevance + exclusion
Compare a treated & untreated group over time	DiD	Parallel trends
Exploit a cutoff rule	RD	No manipulation at cutoff
Follow units over time	Panel fixed effects	Confounders time-invariant

Start from the variation you have, then pick the design — not the other way round.

If you can…	Use	And must defend
Randomise	RCT	Balance, attrition, spillovers, compliance
Find as-good-as-random variation	IV	Relevance and exclusion
Compare groups over time	DiD	Parallel trends
Exploit a cutoff	RD	No manipulation; local validity
Follow units over time	Fixed effects	No time-varying confounders

Read the right-hand column as the questions to ask of any paper. Identifying the design tells you immediately which single assumption the entire result rests on.

The designs are not ranked. An RD with a clean cutoff is often more credible than a poorly executed RCT with heavy differential attrition, and the hierarchy depends on execution.

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The Essential Books

Angrist & Pischke

Mostly Harmless Econometrics — Angrist & Pischke (the design-based bible; RCT, IV, DiD, RD)
Mastering 'Metrics — Angrist & Pischke (gentler, intuitive introduction — start here)
Causal Inference: The Mixtape — Scott Cunningham (free online, code-rich)

If you read one book, read Mastering 'Metrics. It teaches the five core designs in this course with humour and real studies.

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Development Reading

Evidence in development

Poor Economics — Banerjee & Duflo (RCTs and the lives of the poor)
Running Randomized Evaluations — Glennerster & Takavarasha (a practical RCT field guide)
J-PAL & Innovations for Poverty Action (IPA) — policy briefs and evidence syntheses

Read the methods section of real studies critically — it is the fastest way to internalise the ideas in this deck.

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The Takeaways

If you remember five things

Always ask 'compared to what?' — causation needs a counterfactual
Correlation is not causation — suspect selection and confounding first
Design beats adjustment — RCT, IV, DiD, RD, fixed effects each build a comparison
Every method has ONE load-bearing assumption — know it, and interrogate it
Read the standard errors and the robustness — precise is not the same as right

Takeaway	The mistake it prevents
Ask "compared to what?"	Treating a before-after change as an effect
Suspect selection first	Reading programme placement as programme impact
Design beats adjustment	Believing controls remove confounding
Find the load-bearing assumption	Accepting a result without knowing what it rests on
Precision is not validity	Trusting a tight interval around a biased estimate

The fourth is the reading skill worth practising. For any empirical claim, name the design, name its assumption, and ask what would break it — three questions that separate credible work from the rest.

You do not have to run these methods to use them. Most practitioners consume econometrics rather than produce it, and knowing what to interrogate is the more valuable half.

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Where Next

Keep building

Econometrics is learned by doing. Take a real Indian dataset, pose a causal question, and ask which design its variation can support — then stress-test the assumption that design relies on.

Pair this deck with ImpactMojo's Data Literacy, Impact Evaluation and Exploratory Data Analysis 101 courses.

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Econometrics 101 · Complete

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