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.

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

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.

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.

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.

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.

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

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

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.

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).

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.

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.

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.

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.

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

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.

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.

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.

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.

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

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

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.

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

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.

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.

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.

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.

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.

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'.

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.

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.

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.

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.

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.

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.

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.

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.

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

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.

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.

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

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.

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.

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

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.)

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.

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.

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.

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.

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.

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.

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.