Overview
Reviewers in economics, policy, health and management now routinely ask 'what is your identification strategy?' Each quasi-experimental method answers that question differently. Instrumental variables use a source of variation that affects the outcome only through the treatment. Difference-in-differences compares changes over time between treated and untreated groups. Regression discontinuity exploits a cut-off rule. Matching and weighting balance observed characteristics between groups.
Each approach comes with assumptions and failure modes. Weak instruments bias IV towards OLS; two-way fixed effects DiD can give misleading estimates when treatment is staggered and effects vary over time; RDD results can hinge on bandwidth choice; matching cannot fix selection on unobservables. We make these issues visible and use current estimators and diagnostics to address them.
You receive a documented design memo, estimation code, diagnostic plots and tables, and explanations that help you defend the design in a viva, seminar or response to reviewers.
Who it’s for and the problems it solves
This is for you if you are…
- Doctoral students and researchers evaluating policies, reforms or programs
- Economics and finance researchers facing endogeneity concerns from reviewers
- Health services and education researchers using administrative or registry data
- Evaluation teams in public bodies and NGOs needing rigorous impact estimates
Common problems we help with
- A reviewer says your regressor is endogenous and asks for an instrument
- Your first-stage F-statistic is low and you are unsure what that means
- Your policy was adopted by different regions in different years
- The pre-trends in your event-study plot do not look flat
- Your RDD estimate changes sign at different bandwidths
- After matching, some covariates are still imbalanced
What’s included — and what isn’t
Included
- Design consultation: which identification strategy suits your question, setting and data
- IV/2SLS and LIML with first-stage diagnostics, weak-instrument-robust inference and overidentification tests
- GMM estimation for IV and dynamic settings, with Hansen J tests and instrument-count discipline
- Classic 2×2 and multi-period difference-in-differences with clustered standard errors
- Parallel-trends evidence through event-study plots and sensitivity analysis
- Staggered-adoption estimators such as Callaway–Sant'Anna, Sun–Abraham and imputation-based approaches, with Goodman-Bacon decomposition of TWFE
- Sharp and fuzzy regression discontinuity with data-driven bandwidths, manipulation tests and covariate balance at the cut-off
- Propensity score matching, inverse probability weighting and doubly robust estimators with balance diagnostics
- Sensitivity analysis for unobserved confounding where the design relies on selection on observables
- Code in Stata, R or Python with figures ready for papers
Not included
- Searching for an instrument or bandwidth that produces a desired result
- Presenting untestable assumptions as though they had been proven
- Writing your paper or thesis chapters for you
- Legal or regulatory opinions about the policy being evaluated
What you receive
- Identification memo
- The causal question, estimand (for example, ATT or LATE), strategy, key assumptions and how each will be assessed, agreed before estimation.
- Estimation results
- Main estimates with clustered or robust standard errors and confidence intervals, alongside naive OLS for comparison.
- Diagnostics pack
- First-stage tables, event-study plots, RD plots and density tests, or balance tables and love plots, depending on the method.
- Robustness appendix
- Alternative specifications, placebo tests, bandwidth or caliper sensitivity and alternative estimators.
- Reproducible code
- Commented Stata, R or Python code with package versions recorded.
How it works
Frame the causal question
We define treatment, outcome, population and the estimand you actually need.
Choose the design
We assess which strategies your data can support and discuss their assumptions with you.
Build the analysis sample
Treatment timing, control groups, running variables or matching covariates are constructed and documented.
Estimate and diagnose
We run the main models and every relevant diagnostic before interpreting results.
Stress-test and report
Robustness and placebo checks, tables and figures, then a walkthrough of the results.
Designs, estimators and diagnostics
- Instrument relevance
- First-stage F-statistics and effective F (Montiel Olea–Pflueger) for heteroskedastic or clustered errors; Anderson–Rubin confidence sets when instruments may be weak.
- Instrument exogeneity
- Exclusion restrictions cannot be tested directly; we assess them through institutional argument, overidentification tests (Hansen J) where there are extra instruments, and plausibly-exogenous sensitivity bounds.
- Difference-in-differences
- Estimates treatment effects under parallel trends; event-study leads show pre-treatment differences, and HonestDiD-style sensitivity analysis shows how robust conclusions are to violations.
- Staggered adoption
- Callaway–Sant'Anna group-time ATTs, Sun–Abraham interaction-weighted estimates or imputation estimators avoid comparisons that use already-treated units as controls.
- Regression discontinuity
- Local polynomial estimation with MSE-optimal bandwidths and robust bias-corrected intervals (rdrobust), McCrary or rddensity manipulation tests and placebo cut-offs.
- Propensity score methods
- Nearest-neighbor, caliper or kernel matching and IPW, judged by standardized mean differences (commonly below 0.1), variance ratios and overlap plots.
Instrumental variables: relevance and exogeneity
A good instrument must strongly predict the endogenous variable (relevance) and affect the outcome only through it (exogeneity). Relevance can be measured; exogeneity mostly has to be argued. Weak instruments bias 2SLS towards OLS and make standard confidence intervals misleading, so we report first-stage strength using statistics appropriate to your error structure and, where needed, weak-instrument-robust inference.
We also explain what IV estimates: with heterogeneous effects, a local average treatment effect for 'compliers' whose treatment status is moved by the instrument — not necessarily the effect for everyone.
Difference-in-differences with staggered timing
When units adopt a policy at different times and effects change over time, the traditional two-way fixed effects regression can weight some comparisons negatively and produce estimates with the wrong sign. Methods developed since around 2018 — including Callaway and Sant'Anna's group-time average treatment effects (available as did in R and csdid in Stata), Sun and Abraham's interaction-weighted estimator, and imputation approaches — address this by comparing each cohort only with valid controls.
We show the Goodman-Bacon decomposition of your TWFE estimate to reveal whether this matters in your data, present event-study plots from a heterogeneity-robust estimator, and discuss the choice of never-treated versus not-yet-treated controls. Parallel trends is an assumption about the unobserved counterfactual: flat pre-trends support it but cannot prove it, so we add sensitivity analysis rather than relying on a pre-trend test alone.
RDD and matching: local and conditional claims
A regression discontinuity estimates an effect for units near the cut-off. We use data-driven bandwidths, show results across a range of bandwidths and polynomial orders, check for bunching at the threshold and confirm that predetermined covariates do not jump. For fuzzy designs we treat the cut-off as an instrument for take-up.
Propensity score matching balances observed covariates but assumes no unobserved confounders. We report balance before and after matching, trim regions without common support and run sensitivity analyses (for example, Rosenbaum bounds or E-values) so readers can judge how strong hidden bias would need to be to change conclusions.
- Every design yields a specific estimand — ATE, ATT, LATE or a local effect at the cut-off — and we name it
- Placebo outcomes and placebo timing help rule out alternative explanations
- Many robustness checks invite cherry-picking, so all are reported
What the work can look like
Illustrative example — fictional data
Sample excerpt: staggered minimum-wage increases
A researcher studied how regional minimum-wage increases, adopted in different years by 14 of 40 regions, affected youth employment, 2010–2023. All figures are invented.
TWFE versus robust estimator
The conventional TWFE estimate was −0.4 percentage points (SE 0.6). A Goodman-Bacon decomposition showed 31% of the weight came from comparisons using earlier-treated regions as controls. The Callaway–Sant'Anna overall ATT, using never-treated regions, was −1.3 points, 95% CI [−2.4, −0.2].
Pre-trends
Event-study leads were small and jointly insignificant (p = .52). Sensitivity analysis showed the negative effect remained significant unless post-treatment trend violations exceeded about half the largest pre-period deviation.
Interpretation
The effect is described as the average effect on treated regions, with a caution that regions choosing to raise wages may differ in ways that also shifted later trends.
Illustrative example with invented numbers; not a real client project or policy advice.
What you’ll need to provide
- The causal question and background on the policy, program or decision
- Data with treatment timing, outcomes and covariates (anonymized)
- Institutional details: eligibility rules, cut-offs, rollout schedule
- Candidate instruments and the argument for their validity, if any
- Reviewer comments or reference papers using similar designs
You don’t need everything ready to ask for a quote — tell us what you have and we’ll say what’s missing.
What affects price and turnaround
Price depends on
- The design and number of estimators to compare
- Data assembly: constructing treatment timing, control groups or running variables
- Extent of diagnostics, sensitivity and placebo analyses
- Whether a design consultation alone, or full estimation, is needed
- Delivered analysis or guided sessions
Turnaround depends on
- Clarity of treatment definitions and institutional details
- Data size and cleanliness
- Number of robustness checks requested by reviewers
Every project is quoted individually. How we price our work.
Questions people ask before starting
Can you find an instrument for me?
We can help you assess candidate instruments and search the literature in your area for credible ones, but a valid instrument depends on institutional knowledge of your setting. We will be honest if no convincing instrument is available and suggest alternative designs.
Is a first-stage F above 10 enough?
The F > 10 rule is a rough guide derived under specific assumptions. With clustered or heteroskedastic errors, effective F statistics and weak-instrument-robust intervals are more appropriate, and recent work suggests higher thresholds for reliable standard 2SLS inference.
My policy started at the same time for everyone. Do I need the new DiD estimators?
If there is a single adoption date and you use a simple treated-versus-control comparison, the classic DiD is fine. The newer estimators matter mainly for staggered timing with effects that change over time.
Can matching prove causality?
No method proves causality from observational data. Matching makes groups comparable on observed characteristics; we pair it with sensitivity analysis to show how robust results are to unobserved differences.
Which software do you use?
Stata (ivreg2, csdid, rdrobust, teffects), R (fixest, did, rdrobust, MatchIt) or Python. Stata's recent releases include built-in heterogeneous DiD tools, which we use where suitable.
Can you help me respond to reviewers about endogeneity?
Yes. We analyze the concern, run the additional analyses that address it and help you draft a technical response that you then finalize and submit.