11  Causal Inference II: Difference-in-Differences

11.1 What would have happened otherwise

Chapter 10 recovered a causal effect by assuming that the variables driving treatment were all observed, and then conditioning on them. That assumption is untestable and, in most settings, false — countries do not adopt policies for reasons that are fully captured by three indicators.

This chapter takes the opposite route. Rather than measuring the confounders, it uses timing to remove them: if a country’s unobserved characteristics are stable over a short window, then comparing that country to itself before and after differences them away. The remaining problem — that things change over time for everyone — is handled by a second comparison, against units that did not adopt.

Two differences, hence the name.

John Snow** · **1813–1858.

John Snow · 1813–1858

Mapped cholera deaths in 1854 and read a natural experiment off the water supply — before the statistics existed to justify it.

unknown, Autotype 1856, published in 1887. Public domain, via Wikimedia Commons.

From the archive · Snow, 1855

John Snow is remembered for the Broad Street pump, which is the wrong story. The map of cholera deaths clustered around one pump was suggestive, but a sceptic could reply that the people near the pump were poorer, more crowded, and different in a dozen ways from those further off — the selection problem of chapter 10, in 1854.

His second study answered that objection, and it is the one that matters here. Two companies supplied water to overlapping districts of south London, their pipes running down the same streets so that neighbouring houses drew from different sources. In 1852 one of them, Lambeth, moved its intake upstream of the sewage outflows; the other, Southwark and Vauxhall, did not. Snow could therefore compare cholera mortality in households that differed in water supply but not, in any systematic way, in anything else — and compare the change over time between the two.

He called it “an experiment on the grandest scale”, and was explicit that its force came from the assignment: no one chose their supplier, the pipes had been laid years earlier for commercial reasons unrelated to the disease. That is the argument every difference-in-differences paper is still making. Snow made it before the germ theory of disease existed — he had no mechanism, only a design.

11.2 The two differences

Let \(\bar Y_{g,t}\) be the average outcome for group \(g\) in period \(t\), with \(g \in \lbrace\text{treated}, \text{control}\rbrace\) and \(t \in \lbrace\text{pre}, \text{post}\rbrace\). The estimator is

\[ \widehat{\text{DiD}} = \underbrace{\big(\bar Y_{\text{tr,post}} - \bar Y_{\text{tr,pre}}\big)}_{\text{change among the treated}} - \underbrace{\big(\bar Y_{\text{co,post}} - \bar Y_{\text{co,pre}}\big)}_{\text{change among the controls}} . \]

The first difference removes everything time-invariant about the treated group, observed or not — its wealth, its institutions, its geography. The second estimates what would have happened anyway, and subtracting it removes any shock common to both groups.

What licenses the subtraction is a single assumption, and it is worth stating in its exact form because the loose version is misleading.

Parallel trends — in the absence of treatment, the average outcome of the treated group would have followed the same trajectory as the control group. Formally, \[ \mathrm{E}[Y_{\text{tr,post}}(0) - Y_{\text{tr,pre}}(0)] = \mathrm{E}[Y_{\text{co,post}}(0) - Y_{\text{co,pre}}(0)] . \] It is not an assumption that the groups are similar — they may differ by any amount in level — only that the gap between them would have stayed constant.

The assumption concerns \(Y(0)\) for the treated group in the post period, which is precisely the counterfactual that does not exist. Parallel trends is therefore untestable, in the same way and for the same reason as chapter 10’s conditional independence. What can be examined is whether the trends were parallel before treatment, which is evidence about plausibility rather than a test of the assumption itself.

Note also that parallel trends is not invariant to how the outcome is measured. If two groups have parallel trends in levels they generally do not in logs, and vice versa, so the choice of scale is part of the identifying assumption rather than a presentational detail.

11.3 As a regression

The two-by-two table is easier to work with as a regression, and the regression form is one you have already met. With unit and period fixed effects,

\[ Y_{it} \thickspace=\thickspace \alpha_i + \gamma_t + \delta \thinspace D_{it} + \varepsilon_{it}, \]

where \(D_{it}\) is 1 when unit \(i\) is treated in period \(t\), the coefficient \(\delta\) is the difference-in-differences estimate. That is chapter 6’s two-way fixed effects specification with the treatment indicator in place of a continuous regressor: the unit effects absorb the first difference, the period effects the second.

The regression form buys three things — covariates, more than two periods and more than two groups, and standard errors. On the last, chapter 3’s finding returns with force: DiD data are panels, residuals are serially correlated within unit, and treating the country-years as independent understates the standard error badly. Clustering by unit is the minimum, and the classic demonstration of what happens otherwise is Bertrand, Duflo and Mullainathan’s, cited in chapter 3.

11.4 When treatment arrives at different times

The clean two-by-two case has one treatment date. Real policies arrive in different years for different units — which is exactly what the course fixture contains — and for two decades the profession simply put a treatment dummy into a two-way fixed effects regression and read off the coefficient.

That turns out to be wrong in a way nobody noticed until recently. With staggered timing, the TWFE estimate is a weighted average of all the two-by-two comparisons available in the data, and some of those comparisons use already-treated units as controls for later-treated ones. When effects vary over time — when the policy’s impact grows, say — those comparisons subtract a treatment effect rather than a counterfactual trend, and the implied weights can be negative (Chaisemartin and D’Haultfœuille 2020; Goodman-Bacon 2021). A weighted average with negative weights can lie outside the range of the things being averaged, so the estimate can have the wrong sign while every underlying effect has the right one.

The remedy is to build the average yourself: estimate each cohort’s effect against clean controls — units not yet treated, or never treated — and aggregate with weights you chose (Callaway and Sant’Anna 2021; Sun and Abraham 2021).

11.5 The data, and what it will and will not support

Run it: the adoption structure 
import sys, warnings
sys.path.insert(0, "../slides"); sys.path.insert(0, "..")
warnings.filterwarnings("ignore")
from plotstyle import setup, CL
plt = setup()

import numpy as np, pandas as pd, statsmodels.api as sm, qmib

Y, D = "ai_use_any", "has_ai_strategy"
TRUE_EFFECT = 2.4               # from scripts/build_spine/make_fixtures.py

wide = qmib.load("angle_c_country")

# Adoption year must come from the FULL treatment series, not from the rows where
# the outcome happens to be observed. Two countries adopted in 2022 and have a
# missing 2022 outcome; taking the first year they are *seen* treated would put
# them in the 2023 cohort and silently misdate the policy.
adopted = wide[wide[D] == 1].groupby("geo")["time"].min()

panel = wide[(wide["time"] >= 2021) & wide[Y].notna()].copy()
panel["cohort"] = panel["geo"].map(adopted).fillna(9999).astype(int)

print(f"country-years with the outcome observed: {len(panel)}")
print(f"the outcome exists only from {int(panel.time.min())} — "
      f"the AI module did not exist before it\n")
print(f"{'cohort':>10}{'countries':>11}   pre-periods available")
for c in sorted(panel["cohort"].unique()):
    n = panel.loc[panel["cohort"] == c, "geo"].nunique()
    if c == 9999:
        print(f"{'never':>10}{n:>11}   —")
    else:
        pre = [int(t) for t in sorted(panel.time.unique()) if t < c]
        shown = ", ".join(str(t) for t in pre) if pre else "(none)"
        print(f"{c:>10}{n:>11}   {len(pre)}  {shown}")
country-years with the outcome observed: 112
the outcome exists only from 2021 — the AI module did not exist before it

    cohort  countries   pre-periods available
      2021          8   0  (none)
      2022          9   1  2021
      2023          1   2  2021, 2022
     never         12   —

Three facts from that table decide what is possible, and each is a constraint a real analyst meets constantly.

The 2021 cohort cannot be used at all. The outcome series begins in 2021 and those countries adopted in 2021, so there is no pre-treatment observation. No before, no difference, no difference-in-differences. Their data are not weak evidence — they are no evidence for this design.

The 2023 cohort is one country. An estimate from it is a single country’s trajectory, and its standard error would be a fiction.

There is a trap in even getting this table right. Two countries adopted in 2022 and have no 2022 outcome recorded, so if the adoption year is taken from the rows where the outcome is observed — the obvious way to write it — they are assigned to the 2023 cohort and the policy is misdated by a year. The cohort must be read from the treatment series, which is complete, rather than from the analysis sample, which is not.

The 2022 cohort has exactly one pre-period. That is enough to compute the estimator and not enough to examine pre-trends, which needs at least two pre-periods to have a trend to look at.

11.6 The estimates

Run it: TWFE against cohort-by-cohort DiD 
def twoby(cohort, pre, post):
    """Clean 2x2: one cohort against the never-treated, two periods.

    Returns NaN when either group is unobserved in either period — a small
    cohort can simply be absent from a year, and that is not an estimate of zero.
    """
    sub = panel[panel["cohort"].isin([cohort, 9999]) & panel["time"].isin([pre, post])]
    tr = sub[sub["cohort"] == cohort].groupby("time")[Y].mean()
    co = sub[sub["cohort"] == 9999].groupby("time")[Y].mean()
    if not {pre, post} <= set(tr.index) or not {pre, post} <= set(co.index):
        return float("nan")
    return (tr[post] - tr[pre]) - (co[post] - co[pre])

# The specification two decades of papers used.
design = pd.concat([
    panel[[Y, D]].reset_index(drop=True),
    pd.get_dummies(panel["geo"], drop_first=True, dtype=float).reset_index(drop=True),
    pd.get_dummies(panel["time"], prefix="yr", drop_first=True, dtype=float).reset_index(drop=True),
], axis=1)
twfe = sm.OLS(design[Y], sm.add_constant(design.drop(columns=[Y]))).fit(
    cov_type="cluster", cov_kwds={"groups": panel["geo"].reset_index(drop=True)})

print(f"{'estimator':44}{'estimate':>10}{'bias':>9}")
print(f"{'the truth (from the generator)':44}{TRUE_EFFECT:>10.3f}{0.0:>9.3f}")
print(f"{'two-way fixed effects, all cohorts':44}"
      f"{twfe.params[D]:>10.3f}{twfe.params[D] - TRUE_EFFECT:>9.3f}"
      f"   (SE {twfe.bse[D]:.3f})")

print(f"\nclean 2x2 estimates, cohort against never-treated:")
clean = []
for cohort, pre in ((2022, 2021), (2023, 2022)):
    n = panel.loc[panel["cohort"] == cohort, "geo"].nunique()
    for post in range(cohort, 2025):
        v = twoby(cohort, pre, post)
        label = f"   cohort {cohort} ({n} countr{'y' if n == 1 else 'ies'}), {pre}→{post}:"
        if np.isnan(v):
            print(f"{label} not estimable (a group is unobserved that year)")
            continue
        clean.append((cohort, post, v, n))
        print(f"{label} {v:+7.3f}   bias {v - TRUE_EFFECT:+7.3f}")

usable = [v for c, _, v, n in clean if n > 1]
print(f"\naveraging only the cohort with more than one country: "
      f"{np.mean(usable):+.3f}   bias {np.mean(usable) - TRUE_EFFECT:+.3f}")
estimator                                     estimate     bias
the truth (from the generator)                   2.400    0.000
two-way fixed effects, all cohorts               2.811    0.411   (SE 0.834)

clean 2x2 estimates, cohort against never-treated:
   cohort 2022 (9 countries), 2021→2022:  +1.701   bias  -0.699
   cohort 2022 (9 countries), 2021→2023:  +2.702   bias  +0.302
   cohort 2022 (9 countries), 2021→2024:  +2.292   bias  -0.108
   cohort 2023 (1 country), 2022→2023:  +1.666   bias  -0.734
   cohort 2023 (1 country), 2022→2024: not estimable (a group is unobserved that year)

averaging only the cohort with more than one country: +2.232   bias -0.168

The two-way fixed effects estimate is close to the truth here, and it would be dishonest to stage a dramatic failure that the data do not produce. With four periods and effects that are roughly constant once treatment begins, the negative-weighting problem is mild. The point stands anyway: the estimate is close for reasons you can only check by decomposing it, and a paper reporting the TWFE coefficient alone offers no way to know whether its weights were benign.

The cohort estimates show what the decomposition looks like. The 2022 cohort — nine countries with one clean pre-period — gives +1.70, +2.70 and +2.29 in successive years, averaging +2.23 against a truth of +2.40, with the sampling noise you would expect from that many units. The 2023 cohort is a single country; its one estimable comparison happens to land at +1.67, and the second is not estimable at all because that country is absent from the final year. Both are reported rather than quietly dropped, because a cohort of one is a fact about the design and hiding it would make the evidence look stronger than it is.

11.7 The estimator has a name

The loop in that cell is not an improvisation. Estimating each cohort against a clean comparison group and aggregating with weights you chose is precisely the procedure of Callaway and Sant’Anna (2021), and there is a Python implementation of it, diff-diff. It is a young package and the reference implementation is still R’s did, so the first thing to do with it is what this section does: run it beside a calculation you already understand, and find out where the two disagree.

That is worth doing here for three reasons. It states out loud which cells it refuses to estimate. It attaches standard errors to the cohort estimates, which the hand-rolled loop had no way to produce. And it does disagree — in a way that turns out to be the hand-rolled version’s fault.

Run it: Callaway–Sant’Anna on the same panel 
import diff_diff as dd

# The estimator wants one column holding the adoption year, and 0 — not a
# sentinel it would read as a year — for the never-treated.
panel["g"] = panel["cohort"].replace(9999, 0)

cs = dd.CallawaySantAnna(cluster="geo").fit(
    panel, outcome=Y, unit="geo", time="time", first_treat="g")
gt = cs.to_dataframe()

print(f"{'cohort':>7}{'year':>6}{'ATT(g,t)':>10}{'SE':>7}")
for _, r in gt.iterrows():
    g, t = int(r.group), int(r.time)
    if pd.isna(r.effect):
        print(f"{g:>7}{t:>6}{'—':>10}{'—':>7}   dropped: {r.skip_reason}")
    else:
        tag = "  ← pre-treatment, not an effect" if t < g else ""
        print(f"{g:>7}{t:>6}{r.effect:>10.3f}{r.se:>7.3f}{tag}")

print(f"\n{'overall ATT':>18}{cs.overall_att:>10.3f}{cs.overall_se:>7.3f}"
      f"   bias {cs.overall_att - TRUE_EFFECT:+.3f}, {cs.n_clusters} clusters")
for _, r in cs.aggregate("group").to_dataframe().iterrows():
    n = panel.loc[panel["cohort"] == int(r.label), "geo"].nunique()
    print(f"{'cohort ' + str(r.label):>18}{r.att:>10.3f}{r.se:>7.3f}"
          f"   {n} countr{'y' if n == 1 else 'ies'}")

# The hand-rolled estimates and these ones differ. Recomputing each 2x2 over
# only the countries observed in *both* of its two years isolates why.
print("\nthe hand-rolled numbers, and what was wrong with them:")
print(f"{'g,t':>9}{'as written':>12}{'same units':>12}{'ATT(g,t)':>10}")
for g, t in ((2022, 2022), (2022, 2023), (2022, 2024), (2023, 2023)):
    sub = panel[panel["cohort"].isin([g, 9999]) & panel["time"].isin([g - 1, t])]
    seen = sub.groupby("geo")["time"].nunique()
    bal = sub[sub["geo"].isin(seen[seen == 2].index)]
    tr = bal[bal["cohort"] == g].groupby("time")[Y].mean()
    co = bal[bal["cohort"] == 9999].groupby("time")[Y].mean()
    fixed = (tr[t] - tr[g - 1]) - (co[t] - co[g - 1])
    att = gt.loc[(gt.group == g) & (gt.time == t), "effect"].iloc[0]
    print(f"{f'{g},{t}':>9}{twoby(g, g - 1, t):>12.3f}{fixed:>12.3f}{att:>10.3f}")
 cohort  year  ATT(g,t)     SE
   2021  2021         —      —   dropped: missing_period
   2021  2022         —      —   dropped: missing_period
   2021  2023         —      —   dropped: missing_period
   2021  2024         —      —   dropped: missing_period
   2022  2022     1.739  1.135
   2022  2023     2.751  0.843
   2022  2024     2.138  0.977
   2023  2022    -1.126  0.440  ← pre-treatment, not an effect
   2023  2023     1.842  0.553
   2023  2024         —      —   dropped: zero_treated_control

       overall ATT     2.196  0.782   bias -0.204, 30 clusters
       cohort 2022     2.209  0.809   9 countries
       cohort 2023     1.842  0.553   1 country

the hand-rolled numbers, and what was wrong with them:
      g,t  as written  same units  ATT(g,t)
2022,2022       1.701       1.739     1.739
2022,2023       2.702       2.751     2.751
2022,2024       2.292       2.138     2.138
2023,2023       1.666       1.842     1.842

The first table is this chapter’s own reasoning, produced by the estimator rather than argued for in advance. The 2021 cohort is dropped as missing_period — no pre-treatment observation exists, which is the conclusion reached two sections ago by reading the adoption structure. ATT(2023, 2024) is dropped as zero_treated_control, the same absent country the hand-rolled version returned NaN for. Neither refusal is buried inside a coefficient.

The standard errors are new. They come from the influence function of each group-time effect, clustered by country, and they carry through to the aggregate: an overall ATT of +2.20 with a standard error of 0.78, against a truth of 2.40. The interval covers it, which is the honest summary of what thirty countries over four years can establish about an effect of this size.

Read the cohort lines again. The nine-country cohort reports a standard error of 0.81. The one-country cohort reports 0.55. One country’s trajectory is not measured more precisely than nine countries’ — the smaller number is what comes out when there is no between-country variation left to estimate, and the software has no way to know that a cohort of one should not be reported at all. The estimator computes whatever you ask it for. Deciding what is worth asking for is still yours.

The last table is the uncomfortable one. The hand-rolled estimates and Callaway–Sant’Anna’s differ — +1.70 against +1.74, +2.29 against +2.14 — and the middle column says why. twoby averaged whichever countries happened to be present in each year, and this panel is not balanced: Malta and Estonia have no 2022 observation, Luxembourg no 2021, Spain no 2023, Croatia neither. The “before” mean and the “after” mean were therefore computed over different sets of countries, and part of what looked like an effect was the change in who was being averaged. Hold the units fixed and the estimator is reproduced to three decimals.

That failure is on this chapter’s own list — it is the composition change warning further down, committed in code written to demonstrate the method, on a dataset small enough to audit by hand. Which is the argument for using the package rather than the argument against it: not that it is cleverer, but that the choices the hand-rolled version made silently are ones it is forced to make out loud.

11.9 How large a violation would it take?

“The assumption cannot be checked” is where this dataset leaves you. It is not where the literature leaves you. Rambachan and Roth (2023) changes the question: rather than testing parallel trends, ask how large a violation of it would have to be before the finding stops holding, and report that number. The output is a family of intervals indexed by how much post-treatment departure from parallel trends you are prepared to allow — measured, in the relative-magnitudes version, as a multiple \(M\) of the largest departure actually visible before treatment.

Run it: how much violation does the result survive? 
es = cs.aggregate("event_study")

print("the whole of the pre-treatment evidence in this dataset:")
for _, r in es.to_dataframe().query("event_time < 0").iterrows():
    print(f"   event time {int(r.event_time):>3}: {r.att:+.3f}  "
          f"(SE {r.se:.3f}, p {r.p_value:.3f}), from {int(r.n)} cohort")

print(f"\n{'M':>5}{'identified set':>22}{'95% robust CI':>22}   rules out zero")
for M in (0.0, 0.25, 0.5, 1.0, 2.0):
    h = dd.HonestDiD(method="relative_magnitude", M=M).fit(es)
    print(f"{M:>5.2f}   [{h.lb:>7.3f},{h.ub:>7.3f}]     "
          f"[{h.ci_lb:>7.3f},{h.ci_ub:>7.3f}]   "
          f"{'yes' if h.is_significant else 'no'}")
the whole of the pre-treatment evidence in this dataset:
   event time  -1: -1.126  (SE 0.440, p 0.016), from 1 cohort

    M        identified set         95% robust CI   rules out zero
 0.00   [  2.212,  2.212]     [  0.613,  3.812]   yes
 0.25   [  1.649,  2.776]     [  0.050,  4.375]   yes
 0.50   [  1.086,  3.339]     [ -0.513,  4.938]   no
 1.00   [ -0.040,  4.465]     [ -1.640,  6.064]   no
 2.00   [ -2.293,  6.718]     [ -3.892,  8.317]   no

Two things to read off that, and the second matters more.

The pre-treatment evidence is a single number, from a single cohort, and that cohort is a single country. Germany adopted in 2023, so it is the only unit whose pre-period is something other than its own reference year, and its 2021→2022 change ran 1.13 points below the never-treated countries’. Everything in the table below rests on that one comparison. The 2022 cohort, nine countries strong, contributes nothing here at all — its only pre-period is the reference.

The sensitivity table then says: the result survives at \(M = 0.25\) and not at \(M = 0.5\). In words, if post-treatment departures from parallel trends could be as much as half the size of the one pre-treatment departure visible in the data, the interval already contains zero. That is a low breakdown point, and it ought to be — it is what an estimate resting on one country’s single pre-period is worth.

This is not a test, and nothing here has been tested. The honest sentence is “the finding requires post-treatment violations of parallel trends no larger than about a quarter of the single pre-treatment deviation we can observe, and we have one country from which to judge that.” A sensitivity analysis converts an untestable assumption into a statement about how much of it the result needs. That is real progress over asserting the assumption, and it is not the same thing as evidence for it.

11.10 What difference-in-differences cannot fix

Anything that changes at the same time as treatment. Fixed effects remove what is constant; the second difference removes what is common. A shock hitting only the treated group in the treatment year is indistinguishable from the treatment, and no amount of data separates them. Countries that adopt an AI strategy in a given year may be doing several other things that year.

Anticipation. If units change behaviour before adoption because they know it is coming, the pre-period is already contaminated and the “before” is not a clean baseline. This shows as a non-zero pre-trend, when there are enough pre-periods to see one.

Composition change. If the units in the panel change — countries entering or leaving the sample, or a survey changing who it asks — the first difference is comparing different populations rather than the same one over time.

Spillovers. The control group must be unaffected. If a national strategy in one country shifts behaviour in its neighbours, the controls are partially treated and the estimate is attenuated toward zero.

11.11 A short review of the literature

The design is older than its name: Wing, Simon, and Bello-Gomez (2018) traces it to Snow’s 1855 water study and sets out the modern practice, including the pre-trend examination and the sensitivity checks a credible paper is expected to show.

The last decade has been dominated by a single discovery about staggered adoption. Goodman-Bacon (2021) decomposed the two-way fixed effects estimator into the underlying two-by-two comparisons and showed that some of them use already-treated units as controls; Chaisemartin and D’Haultfœuille (2020) showed that the implied weights can be negative, so the estimand may lie outside the range of every underlying effect. Neither paper is a curiosity — between them they called into question a large body of published work.

The constructive replacements estimate cohort-specific effects against clean comparison groups and aggregate them explicitly. Callaway and Sant’Anna (2021) gives the group-time average treatment effects and the aggregation schemes; Sun and Abraham (2021) does the equivalent for event-study specifications, where the same negative weighting contaminates the coefficients on individual leads and lags.

Where the pre-trend evidence is thin — and outside a handful of long panels it usually is — Rambachan and Roth (2023) replaces the ritual pre-trend test with a sensitivity analysis. Report the range of estimates consistent with violations of parallel trends up to a stated size, and the reader can see how much of the assumption the finding actually needs rather than being told it holds.

On inference, the reference remains Bertrand, Duflo and Mullainathan, discussed in chapter 3: DiD data are serially correlated panels, and standard errors that ignore it reject true nulls at many times the nominal rate.

11.12 What to report

  1. The adoption structure. How many units in each cohort, how many periods before and after, and which cohorts are unusable. A table of this is worth more than a paragraph asserting the design is sound.
  2. The parallel-trends argument, as an argument. Why should the gap have stayed constant? Institutional reasoning, not a citation to the assumption.
  3. An event study, with the reference period marked as such — and if there are too few pre-periods to see a trend, say that instead of implying the flat line is evidence.
  4. A staggered-robust estimator alongside TWFE. If they agree, the weights were benign and you have shown it. If they disagree, the decomposition is the finding. diff-diff’s CallawaySantAnna is the Python route; the did package is the R one.
  5. Standard errors clustered by unit, with the number of clusters. Below about forty, say what you did about it.
  6. The scale. Levels or logs is part of the assumption, because parallel trends in one is not parallel trends in the other.
  7. What could have moved at the same time. The most credible DiD papers name the confounding events they considered and explain why each is implausible — which is the modern version of Snow pointing out that nobody chose their water company.
  8. How much violation the result survives. A breakdown value — the size of departure from parallel trends at which the finding stops holding — is worth more than a pre-trend \(p\)-value, and unlike the \(p\)-value it can be reported even when there is nothing to test.
Callaway, Brantly, and Pedro H. C. Sant’Anna. 2021. “Difference-in-Differences with Multiple Time Periods.” Journal of Econometrics 225 (2): 200–230. https://doi.org/10.1016/j.jeconom.2020.12.001.
Chaisemartin, Clément de, and Xavier D’Haultfœuille. 2020. “Two-Way Fixed Effects Estimators with Heterogeneous Treatment Effects.” American Economic Review 110 (9): 2964–96. https://doi.org/10.1257/aer.20181169.
Goodman-Bacon, Andrew. 2021. “Difference-in-Differences with Variation in Treatment Timing.” Journal of Econometrics 225 (2): 254–77. https://doi.org/10.1016/j.jeconom.2021.03.014.
Rambachan, Ashesh, and Jonathan Roth. 2023. “A More Credible Approach to Parallel Trends.” Review of Economic Studies 90 (5): 2555–91. https://doi.org/10.1093/restud/rdad018.
Sun, Liyang, and Sarah Abraham. 2021. “Estimating Dynamic Treatment Effects in Event Studies with Heterogeneous Treatment Effects.” Journal of Econometrics 225 (2): 175–99. https://doi.org/10.1016/j.jeconom.2020.09.006.
Wing, Coady, Kosali Simon, and Ricardo A. Bello-Gomez. 2018. “Designing Difference in Difference Studies: Best Practices for Public Health Policy Research.” Annual Review of Public Health 39 (1): 453–69. https://doi.org/10.1146/annurev-publhealth-040617-013507.