ACADEMIC WRITING GUIDE

How to Conduct and Report a Difference-in-Differences Analysis in a Dissertation (With Worked Examples)

By Acadelyra Editorial TeamPublished

A school introduces an educational support programme and its test scores improve. That improvement alone does not tell you how much the programme helped: scores might also have risen without it. Difference-in-differences (DiD) compares the change in a treated group with the change in a comparison group to address that counterfactual question.

This guide explains how to plan, calculate, estimate and report a DiD analysis in a dissertation. It connects a transparent table to a regression, calculates uncertainty using the correct independent units, and explains why additional periods and staggered adoption require care.

Every school, programme and numerical outcome below is synthetic teaching material. No actual participant findings are reported. The arithmetic has been independently checked in Python and JavaScript. The accompanying R code has been reviewed but was not executed because R was unavailable. Use the reporting examples as models for explaining your own work, subject to your institution's authorship and external-assistance rules.

What is difference-in-differences, and when is it appropriate?

DiD is a research design and family of estimators for comparing outcome changes around an intervention. The canonical design has two groups and two periods: a treatment group observed before and after intervention, and an untreated comparison group observed over the same intervals. Treatment can mean a policy, programme offer or eligibility rule; it need not be a medical treatment.

The comparison group's change supplies an estimate of the treated group's missing change without intervention. This requires a defensible parallel-trends assumption, together with conditions such as no anticipation and no relevant interference between groups. It does not follow automatically from adding an interaction term to a regression.

DiD is useful when intervention timing is clear, comparable outcomes exist on both sides of that timing, and a credible comparison group remains untreated during the relevant comparison. It can accommodate different starting levels. It becomes much less persuasive when the programme coincides with another group-specific reform, measurement changes, or selection driven by a temporary outcome shock. The 2026 practitioner's guide by Baker and colleagues organizes the choice of design, target effect and estimator; these decisions should precede software selection.

Before fitting anything, record the outcome, treatment definition, treatment date, eligible population, comparison group, observation window, weighting rule and target effect in your dissertation data analysis plan. Explain why untreated outcomes would plausibly have evolved similarly. A convenient comparison sample is not sufficient justification.

Define treatment, comparison and the effect you want

Suppose a structured after-school programme is offered in selected schools between two common assessment occasions. The treatment indicator identifies schools offered the programme, including the pre-programme records of those schools. The post indicator identifies the later assessment for both groups. Only their interaction identifies treated schools after the offer begins.

Use administrative implementation records to distinguish announcement, eligibility, actual access and participation. An analysis of programme offer estimates an offer-related effect under its assumptions; relabelling it the effect of attendance introduces a different question and potentially additional selection. Students who voluntarily attend may differ from non-attenders in motivation or need.

The usual target is an average treatment effect on the treated (ATT): the average difference between treated units' outcomes under treatment and their outcomes without treatment. Specify whether units are schools or students. An equally weighted school analysis targets the average school; weighting by enrolment can target a different population. Do not let a default weighting scheme choose the dissertation's substantive question.

Worked example: calculate DiD from a two-by-two table

Our constructed panel contains 40 schools: 20 offered the programme and 20 comparison schools. Each school represents the same 25 students at each occasion, giving 1000 students in total. Outcomes are school mean assessment scores on a common 0–100 scale. Each school receives equal weight. There are 80 school-period records in the two-period analysis; individual student records are not generated or used as independent observations.

No schools or students enter or leave this illustrative panel, and there are no missing outcomes. Real data require explicit verification of those conditions. The treatment group receives the offer after the pre assessment and before the post assessment; the comparison group receives no offer during the window.

Synthetic school mean scores before and after the programme offer
GroupSchoolsPre mean, score pointsPost mean, score pointsPost minus pre, score points
Programme-offer schools2060688
Comparison schools2055583

The treated-group change is 68 − 60 = 8 points. The comparison-group change is 58 − 55 = 3 points. The DiD estimate is (68 − 60) − (58 − 55) = 5 points.

Under parallel trends, the treated group's mean without the programme would have been 60 + 3 = 63 points. Its observed post mean exceeds that counterfactual by 68 − 63 = 5 points. This counterfactual is an assumption-based construction, not an observed untreated outcome for programme schools.

The post-period group difference is 68 − 58 = 10 points. It includes the pre-existing gap of 60 − 55 = 5 points, so it answers a different question from DiD. Nor is the estimate a five per cent improvement: the outcome is a score, and the estimate is in score points.

Three statements that require different evidence
StatementWhat it describesWhat it establishes
Programme schools improved by 8 pointsObserved change within the treated groupImprovement occurred in the constructed records
The DiD estimate is 5 pointsTreated change minus comparison changeA differential change, after subtracting the comparison trend
The programme caused a 5-point average gainA causal interpretation of the differential changeRequires the identifying assumptions and a suitable target population

Fit the matching regression interaction

For school s and assessment occasion t, the canonical model is:

Y_st = beta_0 + beta_T * Treated_s + beta_P * Post_t
       + delta * (Treated_s * Post_t) + error_st

Treated is coded 1 for programme-offer schools and 0 for comparison schools. Post is coded 1 after intervention and 0 before. Include both main effects when fitting this parameterization. With no covariates and consistent equal weighting, the fitted interaction equals the table's DiD estimate.

Coefficients implied by the synthetic two-period means
TermEstimate, score pointsInterpretation
Intercept55Comparison-group pre mean
Treated5Programme-minus-comparison gap before intervention
Post3Comparison-group change
Treated × Post5DiD contrast

Thus the programme post prediction is 55 + 5 + 3 + 5 = 68 points. The Treated coefficient does not estimate the treatment effect: those schools were untreated in the pre period. Likewise, Post does not estimate the programme's effect; it measures the comparison group's change.

With school and occasion fixed effects, the time-invariant treatment-group main effect is absorbed by school effects. In this balanced two-period setting, the treatment interaction still delivers the same contrast. That algebraic equivalence does not justify applying a conventional fixed-effects specification indiscriminately to every adoption pattern.

Calculate uncertainty using schools as the independent units

Four group means alone cannot supply a standard error. You need information about dispersion and dependence. Here we construct individual school changes explicitly. The programme-group changes are 5, 7, 9 and 11 points, each occurring in five schools. The comparison-group changes are 0, 2, 4 and 6 points, again each occurring in five schools. Their respective means are the same 8 and 3 points used above.

For each group, the sum of squared deviations from its change mean is 5 × (9 + 1 + 1 + 9) = 100. Dividing by the group sample size minus one gives a change-score sample variance of 100 / 19 = 5.263158 squared points.

Treating schools as independent, the standard error of the difference in mean changes is:

SE = sqrt(s_T_change^2 / n_T + s_C_change^2 / n_C)

Here SE = sqrt((100 / 19) / 20 + (100 / 19) / 20) = 0.725476 points. A pooled school-change linear model has 40 − 2 = 38 residual degrees of freedom. The two-sided 95% Student-t critical value is 2.024394. Using unrounded inputs, the margin is 1.468650 points and the interval is 3.531350 to 6.468650 points. Rounded for reporting, the estimate is 5.00 points, SE 0.73, with a 95% CI from 3.53 to 6.47 points.

This is a model-based t interval for independent school changes with a common variance; exact t coverage additionally relies on normal change errors. Equal empirical variances in this constructed sample do not prove that assumption in a population. The formula also equals the usual independent-group variance estimate without pooling here because group sizes and sample variances match; unequal samples or variances require an appropriate alternative and degrees-of-freedom rule.

The interval quantifies sampling uncertainty under the working model. It excludes zero, but that does not validate parallel trends or remove confounding. Synthetic data cannot establish that any real programme works. For interval interpretation beyond this example, see confidence intervals in a dissertation.

Why ordinary standard errors can be misleading

Repeated observations from one school are dependent, as may be students within that school. In a longer panel or student-level regression, inference normally needs to account for clustering at the level of treatment assignment and shared shocks, potentially a district above the school. Just clustering on student identifiers would miss common school-level dependence. Bertrand, Duflo and Mullainathan show why ignored serial correlation can badly distort DiD inference; the linked working paper precedes their published 2004 article.

Differencing to one change per school is how this two-period example avoids treating repeated school observations as independent. We use the change regression for uncertainty; the default standard errors from the undifferenced interaction regression are not used. For more complex models, state the covariance estimator, clustering variable, small-sample corrections and number of clusters, including treated clusters. A multilevel model can describe dependence but does not itself establish causal identification; our multilevel modeling guide explains that separate modeling task.

With very few independent clusters, conventional cluster-robust approximations can be unreliable. More students inside the same schools do not create more independent programme assignments. Consider design-appropriate small-sample methods, a suitably justified wild cluster bootstrap, or randomization inference when a known assignment mechanism supports it. There is no universal minimum cluster count that makes every design safe.

Reproduce the school example in R

This base-R script generates the school means directly. It does not generate or claim to analyse raw student records. The within-group baseline offsets sum to zero, while the changes follow the distribution just described. The extra earlier column is used in the next illustration.

# Entirely synthetic, school-level data; no external files needed.
school <- data.frame(
  school_id = seq_len(40),
  treated = rep(c(0, 1), each = 20)
)
school$pre <- 55 + 5 * school$treated +
  rep(seq(-9.5, 9.5, by = 1), times = 2)
school$change <- 3 + 5 * school$treated +
  rep(c(-3, -1, 1, 3), times = 10)
school$post <- school$pre + school$change
school$earlier <- school$pre - 2

# One independent observation per school for the uncertainty model.
change_fit <- lm(change ~ treated, data = school)
estimate <- unname(coef(change_fit)["treated"])
se <- summary(change_fit)$coefficients["treated", "Std. Error"]
ci <- confint(change_fit, "treated", level = 0.95)
print(c(estimate = estimate, SE = se))
print(ci)

# Recover the same point estimate from the interaction regression.
long <- rbind(
  data.frame(school_id = school$school_id,
             treated = school$treated, post = 0, y = school$pre),
  data.frame(school_id = school$school_id,
             treated = school$treated, post = 1, y = school$post)
)
interaction_fit <- lm(y ~ treated * post, data = long)
print(coef(interaction_fit))
# Do not use this model's default SEs for repeated school records.
stopifnot(abs(coef(interaction_fit)["treated:post"] - estimate) < 1e-10)
stopifnot(abs(estimate - 5) < 1e-10)
stopifnot(abs(se - sqrt(10 / 19)) < 1e-10)
stopifnot(max(abs(as.numeric(ci) -
  (estimate + c(-1, 1) * qt(0.975, df = 38) * se))) < 1e-10)

# Common-reference descriptive event-study contrasts.
gaps <- vapply(c("earlier", "pre", "post"), function(v) {
  mean(school[school$treated == 1, v]) -
    mean(school[school$treated == 0, v])
}, numeric(1))
print(gaps - gaps["pre"])
sessionInfo()

These are reproducible instructions, not a pasted R output transcript. The independently verified numerical targets are reported in the prose above. R's official documentation describes linear-model fitting and the Student-t quantile function. In your dissertation, retain the code, input-data provenance, actual output and software versions from your own execution.

Parallel trends concerns untreated potential outcomes: absent the programme, the treated group's average outcome would have changed by the same amount as the comparison group's. It does not require equal starting scores, equal observed post-treatment trends, or identical schools. Observed post trends may diverge precisely because treatment has an effect.

In our example, the identifying claim is that programme schools would have shared the comparison schools' improvement without the offer. The post-intervention untreated outcome of programme schools is unobserved, so that claim cannot be directly tested. A regression fit statistic, balanced baseline table or significant interaction cannot establish it.

Justification combines institutional knowledge, treatment-allocation records, outcome histories and a plausible account of competing changes. Ask whether schools were selected because outcomes had recently fallen, whether staff expected a rebound, and whether resources or assessment rules changed differentially. Stable unobserved level differences can be differenced out; evolving group-specific shocks cannot.

The scale matters too. Parallel trends in scores need not imply parallel trends in log scores or pass rates. Choose a substantively meaningful scale in advance. For a binary outcome, a linear DiD is naturally a difference in probability changes, usually reported in percentage points. A logistic interaction coefficient is on the log-odds scale and is not automatically that probability-scale contrast.

Multiple pre-periods, event studies and diagnostic limits

An earlier assessment can show whether the groups previously moved together. Extend the same synthetic school panel by setting each school's earlier mean to its pre mean minus two points. This adds historical information without changing the two-period estimate or its reported interval.

Synthetic multi-period means and common-reference contrasts
OccasionProgramme meanComparison meanGroup gapGap minus final-pre gap
Earlier pre, event time −2585350
Final pre, event time −1605550, reference
First post, event time 06858105

Both groups gained 2 points between the earlier and final pre assessments. The earlier-pre contrast relative to the final-pre gap is 5 − 5 = 0 points. The post contrast relative to that reference is 10 − 5 = 5 points. The reference-period zero is a normalization, not an estimated null effect. This illustration is deliberately mechanical: every school has the same earlier-to-pre change, so it supplies no realistic pre-trend uncertainty or empirical pre-trend test.

In real data, plot group means and estimate an event study with a clearly identified omitted pre period. Report the event-time window, calendar dates, eligible comparison observations, uncertainty and any endpoint binning. Explain whether pre coefficients compare each occasion with a common reference or with adjacent periods; those are different diagnostics. Post coefficients can describe how effects develop rather than forcing one constant post effect.

A nonsignificant pre-trend test does not prove parallel trends. A test may have insufficient power to detect violations large enough to matter. Roth (2022) also explains that selecting specifications or studies because they pass a pretest can distort subsequent estimation and confidence intervals. Report relevant pre estimates and their uncertainty, discuss substantively meaningful departures, and retain prespecified analyses even when diagnostics are uncomfortable.

When interpreting many event-time coefficients together, distinguish pointwise intervals from simultaneous confidence bands. An isolated significant lead may arise from multiple testing or misspecification; it calls for investigation rather than an automatic verdict. Conversely, wide intervals around near-zero leads are weak reassurance. In staggered designs, use an event-study estimator compatible with heterogeneous effects rather than assuming conventional leads and lags are clean diagnostics.

Threats that belong in the methodology and limitations

Identification threats and practical responses
ThreatEducational-programme exampleWhat to investigate and report
AnticipationSchools change instruction after announcement, before formal launchAnnouncement and exposure dates; a defensible anticipation window and uncontaminated baseline
SpilloversComparison teachers borrow programme materialsGeographic or network exposure; whether the comparison remains untreated in a meaningful sense
Treatment selectionSchools are selected after unusually poor resultsAllocation mechanism, earlier histories, regression to the mean and outcome-driven timing
Concurrent interventionsOnly programme schools also receive new tutoring fundsTiming and reach of each change; inability to separate effects if exposures coincide
Measurement changeProgramme schools switch to an easier assessmentInstrument versions, scoring consistency, testing conditions and common outcome definitions
Composition or attritionLower-scoring students leave programme schoolsWho is observed by group and period; stable eligibility, missingness and changing weights

Do not solve these problems merely by listing them at the end. Use them to decide the sample and estimator. For example, removing nearby comparison schools might reduce spillover exposure, but also change the target population and the credibility of comparison trends. Report the rationale and resulting sample rather than keeping whichever specification gives the preferred coefficient.

If a second intervention always starts in the same schools at the same time, the data may identify a combined package at best. Adding an indistinguishable indicator cannot separate its components. If treatment is triggered by a transitory bad score, a subsequent rebound can mimic a beneficial effect. A fixed effect does not remove this time-varying selection.

Panel data versus repeated cross-sections

A panel follows the same units; repeated cross-sections sample different people at each occasion. Both can support DiD under suitable assumptions, but they support different data preparation and estimation choices. You cannot subtract one student's pre score from another student's post score and call it an individual change.

Our example is a panel of school means with an explicitly stable student cohort. A real school panel can contain changing student samples within each school; keeping the same school identifier does not guarantee stable student composition. Describe both levels. For repeated cross-sections, define the eligible population consistently and examine changes in student characteristics, sampling frames and survey weights. A shift towards higher-scoring entrants can move means without improving any continuing student's outcome.

Covariates, composition and missing data

Pre-treatment characteristics may support a conditional parallel-trends assumption when unconditional trends are implausible. That requires overlap: comparison units with relevant characteristics must exist for the treated population. Inspect the support and weighting distribution, and explain exclusions that change the target sample. Covariate adjustment is not permission to compare fundamentally incomparable groups.

Use covariates whose timing and causal role are defensible. Adjusting for post-treatment attendance could remove part of the programme pathway or introduce selection bias. Simply adding predictors to an ordinary fixed-effects regression does not guarantee the desired ATT under conditional parallel trends; appropriate outcome-regression, weighting or doubly robust DiD procedures make the identifying framework explicit.

Report missing outcomes, school loss and student attrition separately by treatment group and period. Complete-case analysis may select a different population; balancing a panel by dropping incomplete units does not make that selection harmless. Any imputation or attrition weighting must respect the repeated structure, treatment timing and assumptions about missingness. Consult the missing-data dissertation guide when planning the audit trail, then assess whether its assumptions fit the DiD setting. No missing-data procedure automatically restores parallel trends.

Staggered adoption and heterogeneous treatment effects

If schools start the programme in different years, “post” is no longer one common calendar break. Define each school's first treatment period, its cohort of adoption, and the periods during which potential comparison schools remain untreated. Standard staggered-adoption methods usually assume treatment persists once adopted; a programme that switches off or changes dose needs a compatible framework.

The conventional two-way fixed-effects model includes school effects, calendar-time effects and a treatment-status indicator. Goodman-Bacon (2021) explains how the staggered coefficient combines different two-by-two comparisons. Some compare later adopters with already-treated earlier adopters. If earlier adopters' effects are still evolving, subtracting their change also subtracts treatment effects. The resulting coefficient may fail to represent a useful average effect, even when untreated trends are parallel. The linked NBER working paper is the precursor to the verified 2021 journal publication.

Be precise about weights: the decomposition uses nonnegative weights on component two-by-two comparisons in its basic setting, but the implied weights on underlying cohort-time treatment effects can be negative. These are different statements. A decomposition is useful for diagnosing conventional TWFE; it does not itself repair contaminated comparisons.

Sun and Abraham (2021) show a related problem with conventional staggered event studies: a lead or lag can incorporate effects at other relative times, and apparent pre-trends can reflect heterogeneous treatment effects. Their cohort-interacted approach is one alternative when its comparison-group and support conditions fit the question.

Use interpretable group-time effects and deliberate aggregation

Callaway and Sant'Anna (2021) develop effects indexed by first-treatment cohort and calendar period, commonly written ATT(g,t). Each describes the average effect for cohort g at time t relative to its untreated counterfactual. Suitable comparison observations can come from never-treated or not-yet-treated units, subject to the chosen parallel-trends and anticipation conditions.

Not-yet-treated units stop serving as untreated comparisons when anticipation or treatment begins. If everyone eventually adopts, late event times may have no valid untreated support. A software coefficient cannot fill that identification gap. Show cohort sizes, observed periods and which comparisons identify each reported effect.

Choose aggregation to answer the research question: an overall ATT, effects by adoption cohort, calendar-period effects, or effects by time since adoption. State weights and supported horizons. A long-run event-time estimate may involve only early adopters, so differences across event time can partly reflect changing cohort composition. Report a common-support or balanced-horizon analysis where appropriate, with its narrower target population.

The authors' did::att_gt documentation specifies treatment-cohort coding, comparison groups, anticipation, covariates, panel status and clustering. Its aggte documentation explains aggregation and simultaneous bands. In R, a suitable workflow estimates att_gt() and then the prespecified aggte() summaries, explicitly supplying the actual design variables. Use zero to identify never-treated units and positive calendar codes for first treatment. Set panel = FALSE for genuine repeated cross-sections rather than mislabelling repeated school or student records. Record the installed package version and inspect warnings. No staggered model is fitted or numerical staggered result claimed in this guide.

Sensitivity checks and placebo analyses

Choose checks because they probe plausible failures. Useful comparisons include an alternative substantively credible comparison group, an announcement-based anticipation window, an exposure-based spillover exclusion, justified outcome scales, and estimates with and without prespecified baseline adjustment. Explain why each changes the identifying comparison. Sensitivity does not mean searching specifications until one becomes significant.

A pre-intervention placebo date asks whether the design finds a differential change before actual exposure. An outcome the programme should not affect can probe common shocks, provided it is truly unaffected and measured comparably. Such placebos can reveal problems; a null placebo does not validate every identifying assumption. A post-treatment variable on the programme pathway is a poor placebo outcome.

Rambachan and Roth (2023) develop sensitivity analysis that permits specified departures from exact parallel trends. The resulting conclusions depend on substantively defended restrictions on those departures and account for statistical uncertainty. This is more informative than declaring the design valid because pre coefficients are nonsignificant. Do not describe an ordinary trend-adjusted regression as if it were that formal procedure.

Retain a reproducible record of all planned and additional analyses. Report how much the estimate, interval and population change; explain which threats remain unresolved. In the synthetic example, no empirical placebo test, bootstrap or formal sensitivity procedure has been run, and none is implied by the calculated interval.

Dissertation-ready methodology and results paragraphs

The following wording describes the synthetic example only. Replace it with verified details from your approved protocol and executed analysis; do not copy invented school counts or assumptions into a real dissertation.

Methodology example

We illustrated a two-group, two-period difference-in-differences design using constructed school mean assessment scores. The panel comprised 40 schools, with 20 programme-offer schools and 20 comparison schools observed before and after the offer. Each school represented an unchanged cohort of 25 students. Schools were equally weighted, defining a school-average target. The unadjusted estimate compared mean school score changes between groups. Uncertainty was calculated from a linear regression of each school's change on programme-group membership, treating schools as independent and using a common change-error variance and a Student-t reference with 38 degrees of freedom. Causal interpretation would require parallel untreated trends, no anticipation, no relevant spillovers and no differential concurrent intervention or compositional change; these conditions are not established by constructing the example.

Results example

In the synthetic data, programme schools improved from 60 to 68 points and comparison schools from 55 to 58 points. The differential change was 5.00 score points (SE 0.73; 95% CI 3.53 to 6.47), matching the treatment-by-post regression coefficient. This estimate differs from both the programme group's 8-point observed improvement and the 10-point post-period group difference. The interval describes uncertainty under the school-change working model; it does not establish the identifying assumptions or demonstrate an effect of any actual programme. The constructed earlier pre-period contrast was zero by design and provides no empirical validation of parallel trends.

For real data, add recruitment and exclusion counts, treatment dates, missingness, outcome units, adjustment variables, cluster details, diagnostic findings and sensitivity results. Distinguish prespecified from exploratory analyses. The statistical reporting guide can help keep estimates, uncertainty and interpretation aligned across the results chapter, abstract and discussion.

Common reporting mistakes to avoid

  • Calling a treated-group before–after change the DiD estimate.

  • Treating a baseline group difference as evidence against parallel changes, or a nonsignificant baseline difference as evidence for them.

  • Omitting the comparison group's actual trend and leaving readers unable to reconstruct the estimate.

  • Reporting a significant interaction as proof that treatment caused the change.

  • Claiming parallel trends was “confirmed” by a nonsignificant pretest.

  • Counting students or repeated records as independent programme assignments.

  • Using already-treated units as controls without considering heterogeneous effects.

  • Reporting only one pooled coefficient when adoption cohorts or exposure durations answer different questions.

  • Hiding attrition, measurement revisions, unsupported horizons or the assumptions behind covariate adjustment.

  • Reporting code-generated values as executed software output when the code has not been run.

Frequently asked questions

Can I use DiD when the groups start at different levels?

Yes. Different levels are compatible with parallel changes in untreated outcomes. Explain the starting gap and why it would not generate different untreated changes. Selection, ceilings or floor effects can make that argument harder even though equal starting means are not required.

Are two periods enough?

They are enough to calculate the canonical contrast. With just one pre occasion, however, you cannot examine a pre-treatment trend within the observed data. Additional comparable pre periods can strengthen diagnostics and contextual judgment; they cannot reveal the treated group's missing untreated post outcome.

Does a nonsignificant pre-trend test mean I can make a causal claim?

No. It means that particular test did not detect the specified departure at its chosen threshold. Consider the uncertainty, power and substantive size of departures still compatible with the data, alongside the intervention setting and other threats.

Do I need the same students before and after?

Not necessarily. Repeated cross-sectional DiD is possible, but the eligible populations, measurement and sampling processes must remain comparable under the relevant assumptions. Use a suitable estimator and assess composition; individual change-score code requires repeated observations on the same units.

Can I do DiD with one treated school?

You can calculate a contrast, but credible inference and separation of the programme from school-specific shocks become difficult. Hundreds of students do not replace independent treated schools. Discuss an appropriate comparative design and inference strategy with a qualified methods adviser before collecting data.

No. They impose assumptions about how untreated paths extrapolate and may change the target or absorb treatment dynamics. State a substantive rationale and assess sensitivity; do not add trends solely to remove an inconvenient pre-pattern.

Is conventional TWFE always wrong?

No. The simple balanced two-group, two-period case has the transparent equivalence shown here. Problems arise when the fitted specification combines comparisons that do not identify the intended effect, notably staggered timing with evolving heterogeneous effects. Select the estimator from the actual design and target rather than from a universal rule.

What if a modern estimator gives a different answer?

Check the comparisons, weights, sample, adjustment, anticipation window and supported exposure periods. Different answers can reflect different target effects as well as contamination in conventional estimates. Document those differences and choose the method justified by the design, rather than the one with the preferred p-value.

Support for a defensible dissertation analysis

If you need help aligning a DiD design, interpretation and reporting with your research question, explore Acadelyra's academic support services. Appropriate support can explain assumptions, review your analysis plan and improve clarity while you retain responsibility for decisions, executed work and assessed authorship. Follow your institution's rules, acknowledge assistance where required, and never substitute synthetic teaching results for collected evidence.

References and further reading