The Question

Act I

Could a central bank have stopped a banking panic?

In 1930 a Nashville banking giant, Caldwell and Company, collapsed — and bank failures spread across the American South within weeks.

If the Federal Reserve had flooded struggling banks with cash, would more banks have survived, or would the Depression have swept them away regardless?

Open with the stakes: bank runs are contagious. When one big bank fails, depositors everywhere panic and pull their money, and even healthy banks can be forced to close. The policy question — should a central bank act as lender of last resort? — is still debated after every financial crisis (2008, 2020). Ask the room: would emergency lending have helped, or only delayed the inevitable?

A Fed district border split Mississippi into two policy regimes

Same state, same shock, opposite policies — a natural experiment drawn by a map.

The boundary between two Federal Reserve districts runs through the middle of Mississippi. The Atlanta Fed (6th District, southern half) favoured easy credit and liquidity support for banks in trouble. The St. Louis Fed (8th District, northern half) followed the restrictive “Real Bills” doctrine and tightened credit during the crisis. Banks on both sides of the line faced the same local economy — only the policy differed.

Even in the rescue district, banks kept disappearing

Year	6th District (Atlanta Fed)	8th District (St. Louis Fed)
1930	135	165
1931	121	132
1933	102	111

Mississippi banks in business on July 1 of each year.

The Atlanta district lost 33 banks by 1933. Did the rescue fail — or would it have been worse?

This is the naive evidence. Looking only at the treated district, the picture is grim: 135 banks in 1930, 102 by 1933. A before-after comparison would call the Fed’s policy a failure. But the whole country was in the Great Depression. The real question is how many banks the 6th District would have had without the easy-credit policy — and that is something we never observe directly. Full data (banks_clean.csv): 1929 141/169, 1930 135/165, 1931 121/132, 1932 113/120, 1933 102/111, 1934 102/109.

Our route through the chapter

• The question — why one-way comparisons (before vs after, treated vs untreated) mislead
• The investigation — the DD formula and parallel trends; the Mississippi banks; regression DD with fixed effects; the drinking-age case study and its robustness checks
• The resolution — the traps to avoid and what DD can and cannot promise

Learning objectives: explain the difference-in-differences strategy; construct a counterfactual from a control group’s trajectory; state and assess the parallel trends assumption; estimate DD effects with fixed-effects regression; understand why state-specific trends, weighting and clustered standard errors matter; interpret the banking and drinking-age case studies.

Three ideas carry the whole chapter

Counterfactual

The control group’s path stands in for what the treated group would have done untreated.

Parallel trends

Without treatment, both groups would have changed by the same amount — levels may differ.

Panel data

The same units tracked over time; fixed effects absorb constant gaps; DD gives the ATT.

DD trades the coin flip of an experiment for a borrowed trend.

Vocabulary we will use: treatment group vs control group; counterfactual (the unobserved outcome without treatment); parallel trends; before-after comparison; panel data (units × periods); fixed effects (state FE absorb permanent differences, year FE absorb common shocks); serial correlation and clustered standard errors; staggered adoption; ATT — the average treatment effect on the treated, i.e. the effect for the groups that actually received the policy.

The Investigation

Act II

A before-after change bundles the policy with everything else that happened

\[\underbrace{\text{After} - \text{Before}}_{\text{6th District: } -14 \text{ banks}} \;=\; \text{Policy effect} \;+\; \text{Depression trend}\]

From 1930 to 1931 the Atlanta district lost 14 banks — but the Depression was hitting every bank in the country at the same time.

With one group, we cannot tell the policy’s effect from the times it happened in.

The 6th District went from 135 to 121 banks between 1930 and 1931. Some of that decline is the crisis; some of it may be the policy (positive or negative). A before-after comparison cannot separate the two. Analogy: you feel better after taking medicine during flu season — but you might have recovered anyway. We need a comparison group that lived through the same times without the treatment.

Your friend’s weight change reveals what your diet did

	Before → after the holidays	Change
You (on a diet)	gained weight	+2 lbs
Your friend (no diet)	gained weight	+7 lbs
Difference in changes		−5 lbs

Without the diet you would have gained 7 lbs like your friend — so the diet saved you 5.

Naive before-after: you gained 2 lbs, so the diet “failed”. DD: your friend shows what the holidays do to someone who doesn’t diet (+7). Subtract: 2 − 7 = −5. The diet’s effect is 5 lbs less weight gain. The hidden assumption: without the diet, you would have gained the same 7 lbs as your friend. That assumption has a name — parallel trends.

DD subtracts the control group’s change from the treated group’s change

\[\delta_{DD} = \underbrace{\left(\bar{Y}_{\text{treat, after}} - \bar{Y}_{\text{treat, before}}\right)}_{\text{change in treated}} - \underbrace{\left(\bar{Y}_{\text{control, after}} - \bar{Y}_{\text{control, before}}\right)}_{\text{change in control}}\]

Two differences: first over time within each group, then across the groups.

The control group’s change is our estimate of what time alone would have done to the treated group.

δ_DD is the difference-in-differences estimate. Each bracket is a before-after change for one group. In the diet example: (+2) − (+7) = −5. In the banking example the outcome Y is the number of banks in business.

Differencing twice removes both fixed gaps and common shocks

Differencing over time cancels each group’s permanent level; differencing across groups cancels shocks that hit both.

First difference (within each group, over time): any fixed characteristic of a group — size, geography, culture — appears in both “before” and “after” and cancels. Second difference (across groups): any shock common to both groups — the Depression, a recession, national safety campaigns — appears in both changes and cancels. What survives is the treatment effect, provided the groups would otherwise have moved alike.

If the groups would have trended differently anyway, DD absorbs that gap as bias

\[\delta_{DD} \;=\; \text{Treatment effect} \;+\; \underbrace{\left(\text{Trend}_{\text{treat}} - \text{Trend}_{\text{control}}\right)}_{\text{zero under parallel trends}}\]

Parallel trends: absent treatment, both groups would have changed by the same amount.

Parallel trends is the assumption that carries the whole design — and it can never be fully tested.

Runners analogy: two runners on parallel tracks may start at different positions, but without any intervention they run at the same pace. If one suddenly pulls ahead, the intervention caused it. If one was already speeding up before the intervention, DD will wrongly credit that acceleration to the treatment. We can check whether trends were parallel before treatment, but the assumption is about the counterfactual after — which is never observed.

DD needs the same trend, not the same level

Levels in 1930

• Atlanta district: 135 banks
• St. Louis district: 165 banks
• A gap of 30 banks before the crisis

What DD requires

• No need to close the 30-bank gap
• Only that, without the policy, both would have lost banks at the same pace

Groups can start miles apart; they only need to travel in the same direction at the same speed.

A common misconception: “DD needs treatment and control groups that look alike”. It does not — the fixed gap is exactly what the first difference removes. In the one pre-crisis year we have (1929 → 1930), the 6th District went 141 → 135 (−6) and the 8th 169 → 165 (−4): a small, similar drift before the panic. One year is thin evidence, but it is reassuring.

Both districts shrank, but St. Louis shrank far faster

Banks in business in each district, 1929–1934. Solid: actual; dashed: the 6th District’s counterfactual.

After 1930 the tight-credit 8th District lost banks much more quickly than the easy-credit 6th.

Circles: 8th District (St. Louis, tight credit). Squares: 6th District (Atlanta, easy credit). Both lines slope down — the Depression hurt everyone. But the 8th District’s drop between 1930 and 1931 is much steeper (165 → 132) than the 6th’s (135 → 121). The dashed line is the counterfactual we construct on the next slide.

The counterfactual puts the Atlanta district on St. Louis’s path

\[\text{Counterfactual 6th}_t = 135 + \left(\text{8th}_t - 165\right)\]

Year	6th District, actual	6th District, counterfactual
1931	121	102
1932	113	90
1933	102	81
1934	102	79

The gap between actual and counterfactual is the number of banks the policy kept open.

The counterfactual starts the 6th District at its own 1930 level (135) and then subtracts the 8th District’s losses since 1930. This is parallel trends made concrete: “had Atlanta behaved like St. Louis, it would have lost as many banks as St. Louis did”. This is the dashed line in the figure.

DD: the Atlanta Fed kept roughly 19–23 extra banks alive

Year	Change in 6th (treated)	Change in 8th (control)	DD (banks saved)
1931	−14	−33	19
1932	−22	−45	23
1933	−33	−54	21
1934	−33	−56	23

Changes measured relative to 1930.

Easy credit saved about 20 banks — and the gap persisted for years after the panic.

Each DD is (6th change) − (8th change). 1931: (−14) − (−33) = 19. The effect appears immediately and stays in the 21–23 range through 1934: banks that survived the initial panic with Fed support stayed solvent, while illiquid banks that failed in the 8th District did not come back. Relative to the 1930 stock of 135 banks, ~20 is a large share.

A few lines of pandas compute the banking DD

import pandas as pd                       # pandas → load and reshape tables

# every course dataset lives in the repo's data/ folder on GitHub
GITHUB_DATA_URL = "https://raw.githubusercontent.com/cmg777/intro2causal/main/data/"
banks = pd.read_csv(GITHUB_DATA_URL + "ch5/banks_clean.csv").set_index("year")

change_6 = banks["bib6"] - banks.loc[1930, "bib6"]   # treated (Atlanta) change since 1930
change_8 = banks["bib8"] - banks.loc[1930, "bib8"]   # control (St. Louis) change since 1930
dd = change_6 - change_8                             # DD = treated change − control change
print(dd.loc[1931:])                                 # 19, 23, 21, 23 banks saved

↗ Try it in Colab

bib6 and bib8 are banks in business in the 6th and 8th Districts; set_index("year") lets us pick out the 1930 baseline with .loc[1930, ...]. Subtracting a single number from a whole column gives each year’s change relative to 1930. Output: 19 (1931), 23 (1932), 21 (1933), 23 (1934). No regression is needed with two groups — just arithmetic.

With many states and years, DD becomes a regression with fixed effects

\[Y_{st} = \alpha + \delta \, D_{st} + \sum_s \beta_s \, \text{STATE}_s + \sum_t \gamma_t \, \text{YEAR}_t + e_{st}\]

\(Y_{st}\): death rate in state \(s\), year \(t\) (mrate) · \(D_{st}\): treatment (legal) · \(\delta\): the DD effect.

The coefficient \(\delta\) generalizes “treated change minus control change” to many groups and periods.

With two groups and two periods, DD is four numbers and two subtractions. With 51 states that change policy at different times, we let regression do the bookkeeping. The state dummies and year dummies play the role of the two differences; δ is identified by states whose treatment changes relative to the others in the same year.

State effects absorb permanent gaps; year effects absorb nationwide shocks

State fixed effects \(\beta_s\)

• Geography, culture, road quality
• Anything constant over time within a state
• Replaces “before vs after” within each group

Year fixed effects \(\gamma_t\)

• Safer cars, national campaigns, recessions
• Anything that hits every state in a year
• Replaces “minus the control group’s change”

Together they leave only within-state, over-time variation that differs from the national pattern.

Home-court analogy: some teams always do better at home (a team fixed effect), and some seasons are tougher for everyone (a season fixed effect). Remove both, and what’s left can be attributed to a specific coaching change. In pyfixest the fixed effects go after the bar: | state + year. Without state FE, a rural state’s permanently high death rate could be blamed on its drinking law; without year FE, a nationwide decline could be credited to the states that happened to change policy.

Death rates are sticky within a state, so standard errors must be clustered

Standard error for the legal effect	SE	t
Robust, treats every state-year as independent	2.72	3.97
Clustered by state	4.42	2.44

All-cause death rate, state and year fixed effects; estimate 10.80 in both rows.

Ignoring serial correlation would shrink the standard error by nearly 40% — false confidence.

Serial correlation: a state with a high death rate in 1975 probably has a high rate in 1976 too, because demographics and roads change slowly. Fourteen years of one state are not 14 independent pieces of evidence. Clustering by state (vcov={“CRV1”: “state”}) lets errors be correlated within a state; the SE rises from 2.72 to 4.42. Rule: cluster at the level at which treatment is assigned — here, the state. (Numbers from a local re-run of the chapter’s regression with vcov=“hetero” vs clustered.)

States changed their drinking ages at different times

When	What changed
1933	Prohibition ends; each state sets its own drinking age
1970–1975	Many states lower the age to 18, each on its own date
1980s	States raise it back to 21, again at different dates
1984	Federal legislation pushes every state toward 21

Panel: 51 states \(\times\) 14 years (1970–1983) = 714 state-years of death rates for 18–20 year olds.

Staggered adoption creates many treated-vs-control comparisons, not just one.

After Prohibition ended in 1933, states set their own minimum legal drinking age (MLDA). In the early 1970s many lowered it to 18; later many raised it again, and 1984 federal legislation pushed all states to 21 — but states complied at different dates. Each change makes one state “treated” while others serve as controls for that moment. In the data, 32 of the 51 states change their legal value at some point between 1970 and 1983 (local count from deaths_clean.csv).

Treatment is the share of young adults who may legally drink

\[D_{st} = \text{fraction of 18–20 year olds in state } s \text{ allowed to drink in year } t\]

• \(D_{st} = 0\): nobody aged 18–20 may drink · \(D_{st} = 1\): all of them may
• Values in between when the age is 19 or 20, or the law changed mid-year

A continuous dose: \(\delta\) is the effect of moving from no legal access to full legal access.

The variable is called legal. Because laws sometimes set the age at 19 or 20, or changed partway through a year, D is a fraction rather than a 0/1 dummy. About a quarter of the 714 state-years have a value strictly between 0 and 1 (local count). Interpreting δ: the change in deaths per 100,000 when D goes from 0 to 1.

One pf.feols call runs the regression DD

!pip install -q pyfixest                  # pyfixest is not preinstalled in Colab
import pandas as pd                       # pandas → load tables
import pyfixest as pf                     # pyfixest → regressions with fixed effects
GITHUB_DATA_URL = "https://raw.githubusercontent.com/cmg777/intro2causal/main/data/"
deaths = pd.read_csv(GITHUB_DATA_URL + "ch5/deaths_clean.csv")   # state × year × cause
allcause = deaths[deaths["dtype"] == "all"]          # 51 states × 14 years = 714 rows

# death rate on legal-drinking share; absorb state and year fixed effects after "|"
m = pf.feols("mrate ~ legal | state + year", data=allcause,
             vcov={"CRV1": "state"})      # cluster SEs by state
m.summary()                               # legal: 10.80 (SE 4.42)

↗ Try it in Colab

| state + year absorbs the state and year fixed effects without printing 64 dummy coefficients. vcov={"CRV1": "state"} clusters standard errors by state. The file stacks several causes of death (dtype: all, MVA, suicide, homicide, internal, other external), so we filter to one cause first. Output: legal 10.804, SE 4.425, t 2.44, 714 observations.

Legal drinking raised young adults’ death rate by about 11 per 100,000

Outcome: all-cause deaths per 100,000 aged 18–20	Estimate
Effect of full legal access, \(\delta\)	10.80
Standard error (clustered by state)	4.42
t-statistic	2.44

Across specifications the effect ranges from about 8 to 12 deaths per 100,000.

Letting 18–20 year olds drink legally made them measurably more likely to die.

|t| > 2, so the effect is statistically significant. For scale: the average all-cause death rate in this panel is about 136 per 100,000 (local re-run), so ~11 extra deaths is roughly an 8% increase. The 8–12 range comes from the robustness table later (trends: 8.47, weighted: 12.41).

Motor-vehicle crashes account for most of the extra deaths

Cause of death	legal effect (SE)	t
All causes	10.80 (4.42)	2.44
Motor-vehicle accidents	7.59 (2.41)	3.16
Suicide	0.59 (0.57)	1.04
Homicide	0.50 (0.93)	0.54

About 7–8 of the ~11 extra deaths happened on the road.

Same regression, run separately for each cause of death. The mechanism is the most obvious one: legal access to alcohol leads to more drunk driving. Suicide and homicide have plausible alcohol channels (impulsivity, aggression) but show small, insignificant effects. The cause-by-cause pattern tells us how the policy kills, which is itself evidence the result is causal.

Deaths from disease did not respond — the placebo test passes

Cause of death	legal effect (SE)	t
Motor-vehicle accidents	7.59 (2.41)	3.16
Internal causes (disease)	1.33 (1.53)	0.87

Internal causes: cancer, heart disease and other illnesses with no short-run link to legal drinking.

If DD “found” an effect on disease, we would suspect a confounding trend; it finds none.

A placebo (falsification) test runs the design on an outcome the treatment should not affect. If the legal coefficient were large for internal causes, that would suggest states changing their laws were also on different mortality trajectories for unrelated reasons — a parallel-trends violation. A clean placebo doesn’t prove the design valid, but it rules out one important class of threats.

A loop runs the same DD for every cause of death

!pip install -q pyfixest                  # pyfixest is not preinstalled in Colab
import pandas as pd                       # pandas → load tables
import pyfixest as pf                     # pyfixest → regressions with fixed effects
GITHUB_DATA_URL = "https://raw.githubusercontent.com/cmg777/intro2causal/main/data/"
deaths = pd.read_csv(GITHUB_DATA_URL + "ch5/deaths_clean.csv")   # state × year × cause

for cause in ["all", "MVA", "suicide", "homicide", "internal"]:   # one DD per cause
    d = deaths[deaths["dtype"] == cause]                           # keep one cause
    # same regression DD each time: state + year FE, SEs clustered by state
    m = pf.feols("mrate ~ legal | state + year", data=d, vcov={"CRV1": "state"})
    print(cause, round(m.coef()["legal"], 2), round(m.se()["legal"], 2))  # coef, SE

↗ Try it in Colab

Output: all 10.8 (4.42) · MVA 7.59 (2.41) · suicide 0.59 (0.57) · homicide 0.5 (0.93) · internal 1.33 (1.53). m.coef() and m.se() return pandas Series indexed by variable name, so ["legal"] picks the DD coefficient. The placebo row is just another pass of the loop.

Giving each state its own trend barely dents the estimate

Cause of death	Baseline DD	With state-specific trends
All causes	10.80 (4.42)	8.47 (4.90)
Motor-vehicle accidents	7.59 (2.41)	6.64 (2.55)
Internal causes (placebo)	1.33 (1.53)	0.08 (1.86)

Standard errors in parentheses, clustered by state.

The drinking-age effect is a break from each state’s own path, not a pre-existing drift.

State-specific linear trends let every state follow its own straight-line trajectory; δ is then identified only by deviations from that trajectory when the law changes. This is a tougher test of parallel trends. The MVA effect stays large and significant (t ≈ 2.6). The all-cause estimate falls a little and its SE grows — the trends soak up some of the variation. The placebo goes to ~0.

One extra term adds a linear trend for every state

!pip install -q pyfixest                  # pyfixest is not preinstalled in Colab
import pandas as pd                       # pandas → load tables
import pyfixest as pf                     # pyfixest → regressions with fixed effects
GITHUB_DATA_URL = "https://raw.githubusercontent.com/cmg777/intro2causal/main/data/"
deaths = pd.read_csv(GITHUB_DATA_URL + "ch5/deaths_clean.csv")   # state × year × cause
mva = deaths[deaths["dtype"] == "MVA"].copy()         # motor-vehicle deaths only
mva["year_num"] = mva["year"] - 1970                  # years since 1970 (0, 1, …, 13)

# i(state, year_num) gives every state its own linear time trend
m = pf.feols("mrate ~ legal + i(state, year_num) | state + year",
             data=mva, vcov={"CRV1": "state"})        # cluster SEs by state
print(m.coef()["legal"], m.se()["legal"])             # 6.64 (2.55) vs 7.59 without trends

↗ Try it in Colab

i(state, year_num) interacts each state dummy with the year counter: 51 extra slopes. pyfixest prints a harmless warning that one of them is dropped — with year fixed effects in the model, the last state’s slope is collinear with the rest. Centering the year (subtracting 1970) keeps the numbers well-behaved.

Weighting states by population leads to the same conclusion

Cause of death	Unweighted	Population-weighted
All causes	10.80 (4.42)	12.41 (4.43)
Motor-vehicle accidents	7.59 (2.41)	7.50 (2.18)
Suicide	0.59 (0.57)	1.49 (0.85)
Internal causes (placebo)	1.33 (1.53)	1.89 (1.71)

Whether each state or each young person counts equally, the effect is about 7–8 on the road.

Unweighted OLS treats Wyoming and California equally. Weighted least squares (weights = state population of 18–20 year olds) gives large states more influence; their death rates are measured more precisely. The unweighted estimate answers “what is the average effect across states?”; the weighted one answers “what is the effect for the average young person?”. Similar answers mean the effect doesn’t hinge on a few small states. The placebo stays insignificant.

weights="pop" turns the regression into weighted least squares

!pip install -q pyfixest                  # pyfixest is not preinstalled in Colab
import pandas as pd                       # pandas → load tables
import pyfixest as pf                     # pyfixest → regressions with fixed effects
GITHUB_DATA_URL = "https://raw.githubusercontent.com/cmg777/intro2causal/main/data/"
deaths = pd.read_csv(GITHUB_DATA_URL + "ch5/deaths_clean.csv")   # state × year × cause
allcause = deaths[deaths["dtype"] == "all"]          # all-cause death rates

# weights="pop" → weighted least squares: big states count more
m = pf.feols("mrate ~ legal | state + year", data=allcause,
             weights="pop", vcov={"CRV1": "state"})   # cluster SEs by state
print(m.coef()["legal"], m.se()["legal"])             # 12.41 (4.43) vs 10.80 unweighted

↗ Try it in Colab

pop is the state’s population of 18–20 year olds in that year. Everything else — formula, fixed effects, clustering — is unchanged, so any difference in the estimate comes from the weighting alone.

Controlling for beer taxes barely moves the drinking-age effect

Cause of death	legal effect (SE)	Beer-tax effect (SE)
All causes	10.98 (4.52)	1.51 (8.74)
Motor-vehicle accidents	7.59 (2.47)	3.82 (5.20)

State and year fixed effects; SEs clustered by state. Baseline without the control: 10.80 and 7.59.

A policy that changed at the same time does not explain the result away.

Some states changed beer taxes around the same time as their drinking ages. If higher taxes reduce drinking and deaths, omitting them could bias δ. Adding beertax as a control (formula mrate ~ legal + beertax | state + year) leaves the legal coefficient essentially unchanged: 10.80 → 10.98 for all causes, 7.59 → 7.59 for MVA. The beer-tax coefficients themselves are imprecise. (14 state-years with a missing beer tax are dropped.)

Each design buys identification with a different assumption

	RCT (Ch 1)	IV (Ch 3)	RD (Ch 4)	DD (Ch 5)
Key requirement	Random assignment	Valid instrument	Sharp cutoff	Parallel trends
Handles unobservables?	Yes, by randomization	Yes, via the instrument	Yes, at the cutoff	Only time-invariant ones
Estimates	ATE	LATE (compliers)	Local effect at cutoff	ATT (treated group)
Data structure	Cross-section	Cross-section or panel	Running variable	Panel (group \(\times\) time)

DD is the workhorse when policy varies across places and over time but no one flipped a coin.

DD sacrifices the randomization guarantee for much wider applicability: policies change in some places and not others all the time. Its estimate is the ATT — the effect for the states (or districts) that actually received the policy, not for every unit.

Two chapters, one question: age cutoffs versus policy timing

RD (Chapter 4)

• Compares young adults just under vs just over age 21
• Assumption: nothing else jumps at the birthday

DD (Chapter 5)

• Compares states before vs after their laws change
• Assumption: without the change, states trend in parallel

Different designs with different assumptions pointing the same way make the evidence far stronger.

The minimum legal drinking age appears in both chapters. RD exploits the sharp age-21 threshold in one cross-section; DD exploits variation in when states changed their laws. Because the two designs can fail for completely different reasons, finding that legal drinking raises youth deaths with both is much more convincing than either alone.

John Snow used DD logic to trace cholera to dirty water

Water company	Before 1852	After 1852	Cholera deaths
Lambeth (treated)	Polluted stretch of the Thames	Moved intake upstream	Fell sharply
Southwark & Vauxhall (control)	Polluted stretch of the Thames	Same polluted intake	No comparable fall

The change appeared only where the water changed — so cholera traveled by water, not by “bad air”.

Folds both mind-map leaves (Lambeth’s move; deaths dropping only in Lambeth areas). In 1854 London, cholera deaths clustered in neighbourhoods supplied by Southwark and Vauxhall. Lambeth had moved its intake upstream to cleaner water in 1852. Snow compared changes in death rates for the two companies’ customers: two groups, a treatment that changed for one, a comparison of changes. It overturned the prevailing miasma (“bad air”) theory — a DD a century and a half before the name.

The Resolution

Act III

The tempting mistake: “DD needs groups that look alike”

Objection. The Atlanta district had 135 banks and St. Louis 165 — they are too different to compare.

Response. DD differences away any fixed gap. It needs the groups to share a trend, not a level — the 30-bank gap cancels in the first difference.

Students often carry over the RCT intuition that groups must be balanced. In DD, level differences are harmless; what would bias the estimate is a difference in trajectories that has nothing to do with the treatment.

The tempting mistake: “Fixed effects remove every confounder”

Objection. With state and year fixed effects, nothing else can explain the result.

Response. Fixed effects remove only what is constant within a state or common to all states in a year. A state-specific change over time — like a new beer tax — survives them, which is why we add trends, controls and placebos.

Fixed effects are powerful but not magic. Any confounder that varies within a state over time and coincides with the policy change can still bias δ. The robustness checks — state-specific trends, beer-tax control, population weights, placebo outcomes — are how we probe that remaining risk.

Key takeaways

• DD = change in the treated group − change in the control group
• Parallel trends is the assumption that carries the design — same trend, not same level
• Regression DD: state and year fixed effects, standard errors clustered by state
• Banks: the Atlanta Fed’s easy credit kept roughly 19–23 banks in business
• Drinking age: legal access raised youth deaths, mostly on the road — robust to trends, weights and placebos

Back to the opening question: yes — in Mississippi, the district whose Fed lent freely kept about 20 more banks open than the tight-credit counterfactual. And the same logic, scaled up with fixed effects, shows that lowering the drinking age cost young lives, mostly through car crashes.

Recap with the chapter’s visual summary: the question (did the Fed save banks?), the method (compare changes, not levels), the assumption (parallel trends), the tool (regression with state and year fixed effects, clustered SEs), and the evidence (Mississippi banks; drinking age and youth deaths).

When a policy shifts for some groups but not others, the untreated group’s change supplies the missing counterfactual.