The Question

Act I

Is an elite private college worth roughly $20,000 a year more?

Elite private universities charge about $20,000 more per year in tuition than public ones — and their graduates go on to earn substantially more.

Does the school raise earnings, or do its students bring the earning power with them?

Open with the stakes: families borrow heavily for elite tuition on the belief that it pays off. Ask the room: would you pay the premium? Keep the answers in mind — by the end we will see what a careful comparison says.

The raw earnings gap mixes school quality with student quality

No admissions office flips a coin, so there is no experiment to lean on.

Private-college students are smarter, more driven and better connected — they might out-earn others wherever they enrolled.

This is the naive evidence: graduates of top private schools earn more. But the students who get in and enroll differ from public-school students before they ever set foot on campus. The dashed arrow is what we want; the solid arrows through ability and ambition contaminate the raw comparison.

Our route through the chapter

• The question — why the raw private-college premium is not a causal effect
• The investigation — regression with controls; omitted variables bias in a simulation lab; the Dale–Krueger private-college study; sensitivity checks; bad controls
• The resolution — when regression earns a causal reading, and the traps that remain

Learning objectives: explain how regression controls approximate experimental comparisons; write and interpret a regression with treatment and control variables; state the OVB formula and use it to predict the direction of bias; distinguish short and long regressions; recognise bad controls; use sensitivity analysis to judge robustness.

Five terms carry the whole chapter

Term	Plain meaning
Control variable	A pre-treatment trait held fixed in the regression
Ceteris paribus	“Other things equal” — compare people with the same controls
Short vs long regression	Fewer vs more controls; the gap between them reveals bias
Omitted variables bias (OVB)	The distortion from leaving a confounder out
Conditional independence (CIA)	Given the controls, treatment is as good as random

Every slide that follows uses these five ideas.

Other vocabulary we will meet: OLS (ordinary least squares), auxiliary regression, sensitivity analysis, bad control, regression to the mean. Define them as they arrive rather than all at once.

The Investigation

Act II

Choosing a college is Chapter 1’s selection problem — without the lottery

\[\text{Observed gap} \;=\; \text{Causal effect} \;+\; \text{Selection bias}\]

In Chapter 1 random assignment set the selection-bias term to zero. Here, students pick their own schools, so the bias term stays.

We need another way to make the comparison fair: compare students who are alike in the ways that matter.

Same decomposition as Chapter 1. Selection bias = the earnings gap that would exist between private and public students even if the private students had gone public. Ability and ambition make it positive.

Regression works like an automated matchmaker

Alike on paper

• Same test scores
• Same family income
• Same schools applied to

Different choice

• One enrolled private
• One enrolled public
• Compare their earnings

Regression averages the earnings gap across many such matched pairs.

When the matching uses all the right variables, regression approximates what an experiment would show. When an important variable is missing, the match is imperfect and bias creeps back in.

A regression with controls compares students who share the same \(X\)

\[Y_i = \alpha + \beta P_i + \gamma X_i + e_i\]

• \(Y_i\) — earnings (earnings)
• \(P_i\) — 1 if private, 0 if public (private)
• \(X_i\) — a control, e.g. ability (ability)

• \(\beta\) — private effect, holding \(X_i\) fixed
• \(\gamma\) — effect of the control
• \(e_i\) — residual: everything else

\(\beta\) is the private–public gap among students with the same value of the control.

α is the average outcome when P = 0 and X = 0. β is how much Y changes when P switches from 0 to 1 with X held constant — the ceteris paribus effect we are after.

OLS chooses the coefficients that make squared prediction errors smallest

\[\min_{\alpha,\,\beta,\,\gamma}\ \sum_{i=1}^{n} \big(Y_i - \alpha - \beta P_i - \gamma X_i\big)^2\]

Each term in the sum is a squared residual \(e_i^2\): the gap between actual and predicted earnings.

Like a tailor fitting a suit: no single measurement is perfect, but the total mismatch is as small as possible.

OLS = ordinary least squares. Squaring makes large misses count heavily and lets positive and negative errors not cancel. pyfixest’s pf.feols does this minimisation for us.

Controls turn a difference in means into an “other things equal” comparison

Chapter 1

\[Y_i = \alpha + \beta D_i + e_i\] \(\beta\) = treated mean − control mean. Fair because \(D_i\) was randomized.

Chapter 2

\[Y_i = \alpha + \beta P_i + \gamma X_i + e_i\] \(\beta\) = gap within groups that share \(X_i\). Needed because \(P_i\) is chosen.

Controls do for observational data what the lottery did for experiments — if they are the right controls.

Adding controls is the key innovation of the chapter. The regression on a dummy from Chapter 1 is the special case with no X.

Regression is causal only if, given the controls, school choice is as good as random

Conditional independence assumption (CIA): among students with the same controls, who goes private is unrelated to what they would have earned.

\[E[Y_{0i} \mid P_i, X_i] = E[Y_{0i} \mid X_i]\]

Within a cell of identical \(X_i\), private and public students would have earned the same on average without the private school.

The CIA cannot be tested directly — the choice of controls has to be argued for.

Y₀ᵢ is the earnings student i would have had at a public school. If the CIA holds, selection bias disappears within groups that share X, and β is causal. Twin analogy: if the match is perfect, any earnings difference is due to the school.

A simulation plants a true effect of $5,000 — so we can check who finds it

1,000 simulated students · ability has mean 50, sd 10 · abler students are likelier to go private

Because we wrote the rules, we know the right answer: $5,000.

This is a lab with a known truth. In real data the true effect is never known; here we design it so we can see exactly when regression gets it right and when it goes wrong. Ability drives both the school choice and earnings — the textbook confounder.

Ten lines build the simulated students and show the raw gap

import numpy as np                        # numpy → random numbers
import pandas as pd                       # pandas → tables and group means

np.random.seed(42)                        # fix the seed so everyone gets the same draws
n = 1000                                  # 1,000 simulated students
ability = np.random.normal(50, 10, n)     # ability (mean 50, sd 10): the confounder
p_private = 1 / (1 + np.exp(-(ability - 50) / 5))   # abler students lean private
private = np.random.binomial(1, p_private)          # 1 = private, 0 = public
# truth: private adds $5,000; each ability point adds $800; plus noise
earnings = 30000 + 5000 * private + 800 * ability + np.random.normal(0, 5000, n)
students = pd.DataFrame({"earnings": earnings, "private": private, "ability": ability})

students.groupby("private")[["earnings", "ability"]].mean()   # raw gaps by school type

↗ Try it in Colab

This chapter uses simulated data, so there is no file to download — the block builds the dataset itself. Output: public students average $65,387 in earnings and 44.4 ability points; private students average $80,146 and 56.1 points. The logistic function turns ability into a probability of going private; binomial(1, p) flips each student’s personal coin.

The short regression reproduces the raw gap — nearly three times the truth

	Public mean	Private mean	Gap
Earnings ($)	65,387	80,146	14,760
Ability (points)	44.4	56.1	11.7

Short regression earnings ~ private: coefficient 14,760 (robust SE 512) · true effect 5,000

Private students earn more largely because they score 11.7 points higher on ability.

504 simulated students are public, 496 private. A regression of earnings on the private dummy alone — the short regression — returns exactly the difference in means, $14,760, far above the $5,000 we planted. The excess is omitted variables bias: the dummy absorbs ability’s effect.

Holding ability fixed brings the estimate back to about $5,000

Regression	Controls	Private coefficient (robust SE)
Short	none	14,760 (512)
Long	ability	5,079 (391)
Truth	—	5,000

In the long regression each ability point adds $826 (SE 19) — close to the $800 we planted.

Control for the confounder and regression recovers the causal effect.

The long regression includes ability. The private coefficient falls from $14,760 to $5,079, within about one standard error of the truth. (The chapter’s default non-robust SEs are 512 and 382; robust SEs are shown here to match the code.)

Two pf.feols calls contrast the short and the long regression

!pip install -q pyfixest                  # pyfixest is not preinstalled in Colab
import numpy as np, pandas as pd          # numbers + tables
import pyfixest as pf                     # pyfixest → regressions with robust SEs

np.random.seed(42); n = 1000              # rebuild the same 1,000 students
ability = np.random.normal(50, 10, n)     # the confounder
private = np.random.binomial(1, 1 / (1 + np.exp(-(ability - 50) / 5)))   # abler → private
earnings = 30000 + 5000 * private + 800 * ability + np.random.normal(0, 5000, n)  # truth +5,000
df = pd.DataFrame({"earnings": earnings, "private": private, "ability": ability})  # one table

short = pf.feols("earnings ~ private", data=df, vcov="hetero")            # ability left out
long = pf.feols("earnings ~ private + ability", data=df, vcov="hetero")   # ability held fixed
pf.etable([short, long])                  # private: 14,760 (short) vs 5,079 (long)

↗ Try it in Colab

vcov="hetero" asks for heteroskedasticity-robust standard errors. pf.etable lines the two models up side by side: private 14,759.83 (512.185) in the short model; 5,078.71 (390.848) and ability 826.28 (19.121) in the long one. Adding a control is just adding + ability to the formula.

The gap between short and long is the omitted variable’s footprint

\[\text{OVB} \;=\; \beta^s - \beta^l \;=\; \pi_1 \times \gamma\]

• \(\beta^s\), \(\beta^l\) — private coefficient in the short and long regressions

• \(\pi_1\) — how the omitted variable differs with treatment
• \(\gamma\) — its effect on the outcome (long regression)

If either factor is zero — unrelated to treatment, or irrelevant to the outcome — there is no bias.

Baking analogy: forget the sugar (omitted variable). π₁ asks how tightly sugar travels with the ingredients you did include; γ asks how much sugar matters for taste. The distortion is their product.

An auxiliary regression measures how the omitted variable travels with treatment

\[A_i = \pi_0 + \pi_1 P_i + u_i\]

\(A_i\) is ability (ability), regressed on the private dummy \(P_i\).

In the simulation, \(\pi_1 = 11.72\): private students score 11.72 ability points higher than public students.

\(\pi_1 > 0\): the omitted trait rides along with private enrollment.

The auxiliary regression is “auxiliary” because we do not care about it for its own sake — it only supplies the π₁ in the OVB formula. With a dummy regressor, π₁ is just the difference in mean ability between private and public students.

In the simulation the formula matches short minus long exactly

Piece	Value
Short coefficient \(\beta^s\)	14,760
Long coefficient \(\beta^l\)	5,079
OVB, direct: \(\beta^s - \beta^l\)	9,681
\(\pi_1\) (ability on private)	11.72
\(\gamma\) (ability in long regression)	826
OVB, formula: \(\pi_1 \times \gamma\)	9,681

Positive × positive = upward bias: omitting ability made private college look too good.

11.72 × 826.28 ≈ 9,681 — the same number as 14,760 − 5,079. The formula is an algebraic identity for OLS, not an approximation.

Three regressions verify the OVB formula in code

!pip install -q pyfixest                  # pyfixest is not preinstalled in Colab
import numpy as np, pandas as pd          # numbers + tables
import pyfixest as pf                     # pyfixest → regressions with robust SEs

np.random.seed(42); n = 1000              # rebuild the same 1,000 students
ability = np.random.normal(50, 10, n)     # the confounder
private = np.random.binomial(1, 1 / (1 + np.exp(-(ability - 50) / 5)))   # abler → private
earnings = 30000 + 5000 * private + 800 * ability + np.random.normal(0, 5000, n)  # truth +5,000
df = pd.DataFrame({"earnings": earnings, "private": private, "ability": ability})  # one table

short = pf.feols("earnings ~ private", data=df, vcov="hetero")            # short regression
long = pf.feols("earnings ~ private + ability", data=df, vcov="hetero")   # long regression
aux = pf.feols("ability ~ private", data=df, vcov="hetero")               # auxiliary regression
pi_1, gamma = aux.coef()["private"], long.coef()["ability"]               # 11.72 and 826
print(short.coef()["private"] - long.coef()["private"], pi_1 * gamma)     # both ≈ 9,681

↗ Try it in Colab

.coef() returns the estimated coefficients as a pandas Series, indexed by variable name. Both printed numbers are 9,681.12 — identical up to rounding error. The vcov choice does not affect the coefficients, only the standard errors.

Signs alone predict the direction of the bias

\(\pi_1\) (omitted ↔︎ treatment)	\(\gamma\) (omitted → outcome)	OVB direction
Positive	Positive	Upward
Positive	Negative	Downward
Negative	Positive	Downward
Negative	Negative	Upward

You can reason about bias from a confounder you never observe — just argue the two signs.

Example: a job-training study that omits prior experience. Experienced workers are likelier to be trained (π₁ > 0) and earn more (γ > 0), so the training effect is biased upward. If instead weaker students were steered into a program, π₁ < 0 and the bias would be downward.

Dale and Krueger let application choices reveal ambition

• Data: the College and Beyond survey — more than 14,000 college students followed into the labor market
• Insight: the schools a student applies to reveal ambition and ability
• The data are not public, so we discuss their findings; the simulation showed the same mechanics

Applications are a pre-treatment signal of exactly the traits that bias the raw comparison.

Stacy Dale and Alan Krueger studied the earnings of former students using the College and Beyond (C&B) dataset. Their idea: what you aim for says a lot about you — and it is determined before you enroll, so it is a legitimate control.

The self-revelation design: same admissions, different enrollment choice

Two students admitted to both an elite private college and a flagship public university, who chose differently.

Equally qualified on paper — the only difference left is where they enrolled.

Both students passed the same admissions screens, so admissions officers judged them alike. The regression controls for the set of schools applied to and admitted by; within each set, the private–public comparison is close to a matched comparison.

The private premium shrinks from 14% to about zero as the controls sharpen

Comparison	Controls	Private premium
Raw	none	about 14%
Selectivity groups	Barron’s selectivity category	about 7%
Self-revelation	schools applied to and admitted by	close to zero

Each better control strips away more selection bias — OVB at work on real data.

Barron’s ranks colleges by selectivity; controlling for those groups halves the premium. Controlling for the specific schools students applied to — the self-revelation model — removes almost all of it. Exactly the pattern from the simulation: the right control makes the treatment effect collapse.

Most of the elite-college premium is who enrolls, not what the school adds

≈ 0

private-college earnings premium once applications are held fixed (raw gap: about 14%)

Students who aim high do well wherever they end up. The raw earnings advantage of elite private colleges mostly reflects the students they attract, not the education they provide.

Adding SAT scores, parental income and demographics barely moves the estimate

Once the application-set controls are in, piling on further traits leaves the private coefficient nearly unchanged.

Like stress-testing a bridge: if it holds under different loads, we trust it is sturdy.

Stable estimates across specifications build confidence in a causal reading.

This is regression sensitivity analysis. If each added control moved the estimate a lot, we would worry that further unmeasured controls might move it too. Dale and Krueger’s estimate survives.

Given application behavior, the extra traits no longer travel with private enrollment

\[\text{OVB from SAT, income, …} \;=\; \pi_1 \times \gamma \;\approx\; 0 \times \gamma \;=\; 0\]

Among students with the same applications, SAT scores and parental income barely differ between private and public enrollees.

The OVB formula explains the stability: when \(\pi_1 \approx 0\), omitting a trait costs almost no bias.

SAT and income still matter for earnings (γ ≠ 0), but conditional on the application set they are nearly unrelated to the private/public choice, so their product with γ is close to zero.

When each new control moves the estimate a lot, more confounders may lurk

Controls in the regression	Private coefficient
None	18,506
+ ability	12,429
+ ability + family income	8,428
+ ability + family income + motivation	4,720

A simulation with three confounders and a true effect of $5,000.

Big jumps are a warning sign; only the full set of confounders lands near the truth.

The mirror image of Dale and Krueger. Here every confounder pushes students toward private college and also raises earnings, so each omitted one adds its own OVB term. In real data we never know whether the list is complete — which is why instability is a red flag.

A three-line loop runs the sensitivity analysis

!pip install -q pyfixest                  # pyfixest is not preinstalled in Colab
import numpy as np, pandas as pd          # numbers + tables
import pyfixest as pf                     # pyfixest → regressions with robust SEs

np.random.seed(42); n = 1000              # 1,000 students, now with THREE confounders
ability = np.random.normal(50, 10, n)     # confounder 1
income = np.random.normal(60000, 20000, n)   # confounder 2: family income
motivation = np.random.normal(5, 2, n)    # confounder 3
index = (ability - 50) / 5 + (income - 60000) / 20000 + (motivation - 5) / 2   # all push to private
private = np.random.binomial(1, 1 / (1 + np.exp(-index)))                       # 1 = private
earnings = (10000 + 5000 * private + 800 * ability + 0.3 * income        # truth: +5,000 ...
            + 2000 * motivation + np.random.normal(0, 5000, n))          # ... plus confounders
df = pd.DataFrame(dict(earnings=earnings, private=private, ability=ability,
                       income=income, motivation=motivation))            # one table

for x in ["", " + ability", " + ability + income", " + ability + income + motivation"]:
    m = pf.feols("earnings ~ private" + x, data=df, vcov="hetero")  # add controls one by one
    print(x or "none", round(m.coef()["private"]))                  # 18,506 → ... → 4,720

↗ Try it in Colab

The data-building part is longer, but the analysis is the last three lines: build each formula by string concatenation, fit it, print the private coefficient. Output: none 18,506; + ability 12,429; + ability + income 8,428; + all three 4,720.

Controlling for occupation blocks one of the paths a college works through

Holding occupation fixed asks: among people in the same job, do private graduates earn more?

A bad control removes part of the very effect we want to measure — here, biasing it downward.

If private college helps people into better-paid occupations, occupation is an outcome of the treatment, not a confounder. Conditioning on it throws away one of the main channels and distorts the estimate.

Control only for traits fixed before the treatment

Good controls — pre-treatment

• Ability, test scores
• Parental income
• Schools applied to

Bad controls — post-treatment

• Occupation
• Graduate degree
• Industry

Outcomes of the treatment are not confounders. Chapter 6 returns to this trap.

Rule of thumb: only control for variables determined before treatment was assigned. Variables determined afterwards are potential outcomes themselves. Chapter 6 revisits bad controls in the returns-to-schooling setting (controlling for occupation when estimating the effect of education).

Every later method in the course is built on regression

Chapter	How regression appears
1 · Randomized trials	A difference in means is a regression on a treatment dummy
3 · Instrumental variables	First stage and reduced form are regressions; 2SLS uses fitted values
4 · Regression discontinuity	Regression with a polynomial in the running variable
5 · Differences-in-differences	Regression with group and time fixed effects
6 · Wages of schooling	OLS as the baseline; twins fixed effects as a differenced regression

Master pf.feols once and you can run every design in the course.

The formulas change — fixed effects after a |, instruments after another | — but the engine is the same least-squares regression we met today.

Regression began as a tool for description, not causation

When	Who	Contribution
1886	Francis Galton	Tall parents have tall but less extreme children — “regression to the mean”
1899	George Udny Yule	Used several controls at once to study changes in English pauperism

The causal reading of \(\beta\) is modern — it rests on the assumptions of this lecture.

Galton gave the method its name while studying heights across generations — a statistical regularity, not a causal effect. Yule pioneered multiple controls in social policy questions. Neither framed the question “is β causal?” — that depends on the right controls and no omitted confounders.

The Resolution

Act III

The tempting mistake: “Elite graduates earn more, so an elite college pays off”

Objection. Graduates of top private colleges out-earn everyone else, so the tuition must be worth it.

Response. The raw gap is mostly selection. Compare students with the same applications and the premium falls from about 14% to close to zero.

The same correlation-versus-causation trap as Chapter 1’s insurance example. Here OVB from ambition and ability inflates the naive premium.

The tempting mistake: “When in doubt, just add more controls”

Objection. More controls can only make the estimate cleaner.

Response. Only pre-treatment confounders reduce bias. Irrelevant controls waste precision, and bad controls — outcomes of the treatment — create new bias.

Occupation is the canonical bad control in this chapter. The question to ask of every control: was it determined before the treatment, and could it drive both treatment and outcome?

Key takeaways

• Regression compares treated and untreated units with the same controls
• \(\text{OVB} = \pi_1 \times \gamma\) — and the signs predict the direction of bias
• Stable estimates across specifications build confidence
• Never control for outcomes of the treatment
• The private-college premium largely vanishes with the right controls

Back to the opening question: is the elite premium worth $20,000 a year? For students who would be admitted to both kinds of school, the earnings evidence says the premium is mostly who you are, not where you go.

Recap with the chapter’s visual summary: the question (is private college worth it?), the tool (regression holds controls fixed), the risk (omitted variables bias), and the test (sensitivity analysis) — plus the warning about bad controls.

Regression delivers causal effects only when the right pre-treatment controls make treatment as good as random.