ACADEMIC WRITING GUIDE

How to Conduct and Report Propensity Score Matching in a Dissertation (With Worked Examples)

By Acadelyra Editorial TeamPublished

Two adults can enter the same employment-training study with very different prospects. One may already have recent work experience, higher earnings and reliable access to vacancies; another may join because finding work has become difficult. Comparing their later earnings without addressing those differences can mistake selection into training for a programme effect.

Propensity score matching (PSM) constructs a comparison group using measured characteristics recorded before treatment. A defensible dissertation must explain how matches were chosen, whether covariates became balanced, whose effect remains estimable and how uncertainty was handled. Producing a matched dataset is only one stage of that argument.

This guide follows a new, entirely synthetic employment-training study from design to reporting. Its numerical calculations were executed independently in Python and JavaScript. R was unavailable: the R code below has been reviewed against official documentation but has not been executed. The data do not describe actual people, a real programme or evidence of programme effectiveness.

What a propensity score represents

For a binary treatment indicator T and baseline covariates X, the propensity score is e(X) = P(T = 1 given X): the conditional probability of receiving treatment given those measured characteristics. It predicts treatment receipt, not the outcome and not an individual's benefit from treatment.

The balancing-score result in Rosenbaum and Rubin (1983) concerns the true propensity score and the distribution of observed covariates. In practice, scores are estimated, samples are finite and matching is approximate. Similar estimated scores therefore do not guarantee similar covariates. Check the covariates themselves after matching.

Matching can reduce differences in recorded characteristics. It cannot balance an unrecorded characteristic simply because that characteristic matters. An observational comparison does not become a randomized experiment after matching.

Define the treatment, population and estimand first

Suppose Harbour Skills Bridge is a fictional programme open to eligible adults in one recruitment cohort. Treatment is voluntary enrolment at the cohort start; comparison adults are eligible at that same date but do not enrol. The outcome is monthly earnings twelve months after that shared baseline, measured in hypothetical currency units (CU), including zero earnings where relevant. Training completion is not the treatment definition: redefining treatment by later completion would introduce post-baseline selection.

Eligibility, baseline measurement and follow-up must align across groups. Comparing programme starters with people selected only because they remained unemployed at follow-up would create a biased comparison group. Define treatment versions and plausible spillovers too: participants sharing training materials or competing for the same jobs could undermine a simple no-interference assumption.

Write Y(1) for earnings under enrolment and Y(0) for earnings without enrolment. Each person contributes only one observed outcome.

Three different target effects for the same programme
EstimandTarget questionConsequence for matching
ATT: average treatment effect on the treatedWhat was the average effect for adults who enrolled?Use enrollees as the focal group and find nonparticipant comparisons.
ATC: average treatment effect on the controlsWhat would enrolment have changed for the nonparticipants?Reverse the focal group and seek comparable treated adults.
ATE: average treatment effectWhat would change if the eligible target population enrolled rather than did not enrol?Requires support and an estimator targeting that population; ordinary treated-to-control pair matching does not automatically estimate it.

Our initial target is the ATT among eligible enrollees in this cohort. If matching removes some enrollees, the reported target must narrow to the retained treated adults. Selecting estimand = "ATT" in software does not override that change. The current MatchIt effects guide makes this distinction explicit.

This is an analysis-sample decision. Recruiting a representative sample and justifying its size are separate tasks covered in the sampling and sample-size guide.

Decide whether matching is defensible

PSM may be useful when treatment is observational, credible pretreatment confounders are measured, treated and comparison adults have usable overlap, and the dissertation needs a transparent comparison for a stated target. It cannot repair a design in which the key selection process is unknowable or one group has no plausible counterparts.

For causal interpretation, explain conditional exchangeability: after conditioning on the chosen baseline information, treatment receipt would need to be unrelated to the relevant potential outcomes. For the ATT, the key missing comparison is the treated adults' untreated potential outcome. This assumption cannot be proved from a balance table. Consistent treatment definitions, adequate measurement, relevant overlap and suitable outcome follow-up are also needed.

Positivity means that the treatment alternatives needed for the target comparison are possible at the relevant covariate values. For a population ATE, this ordinarily requires probabilities strictly between zero and one throughout the target population. An ATT comparison particularly needs untreated counterparts where treated adults occur. Common support describes the region of observed covariate or score distributions in which comparisons are available. Overlapping score ranges alone can hide sparse regions or poor overlap on individual covariates.

Plot the score distributions separately by group before matching. Look for isolated tails and regions with very few comparison adults. Repeat the plot after matching, using the actual matching weights. Show the changing composition alongside the distributions; a visually similar pair of histograms is not proof of exchangeability.

Other methods may be better. Weighting can retain more observations but may create unstable weights when overlap is weak. Outcome regression models earnings directly but can rely on extrapolation. Matching on covariate distances within a propensity-score caliper may protect important dimensions more directly. These choices require comparison on target, balance and assumptions. King and Nielsen (2019) show that propensity-score pruning can worsen balance; do not assume increasingly aggressive pruning improves the design.

Select genuine pretreatment covariates

Choose covariates from the treatment-selection process and substantive knowledge about earnings, before examining treatment-effect results. A causal diagram and a dated variable dictionary can make the rationale reviewable.

Baseline covariates in the synthetic Harbour Skills Bridge study
VariableCausal rationaleMeasurement boundary
Age in yearsMay influence programme enrolment, hiring opportunities and earnings.Recorded at cohort entry, before enrolment begins.
Months employed in the preceding two yearsPrior labour-market attachment may influence selection and future earnings.The historical window ends before programme start.
Baseline monthly earnings in CUFinancial position and earning capacity may influence enrolment and later earnings.Measured over the same pre-programme reference period in both groups.

These are illustrative measured confounders, not a sufficient adjustment set for every actual training evaluation. Qualifications, health, caregiving and local opportunities could also matter. In a real study, justify inclusion or explain the consequences of their absence.

Do not adjust the propensity model for attendance, completion, post-training qualifications or later job-search intensity when these can be consequences of enrolment. They may be mediators. A variable measured before treatment is not automatically appropriate either: conditioning on a collider can introduce bias, while a strong treatment-only predictor can damage overlap without addressing outcome confounding. Stuart's matching review discusses covariate selection and the separation of design from outcome analysis.

Resolve missing baseline information through a justified, prespecified strategy; do not silently delete incomplete records and retain the original target-population claim. The synthetic example has complete data. Record these choices in the broader dissertation data analysis plan.

Estimate treatment probabilities, then judge balance

A logistic propensity model uses treatment as its dependent variable. Here the predictors are scaled solely for numerical convenience:

eta = b0 + b1 * (age - 38)/10
         + b2 * (months - 12)/12
         + b3 * (baseline - 1000)/1000
propensity score = 1 / (1 + exp(-eta))

The fitted coefficients are b0 = -0.573963, b1 = 0.336365, b2 = 0.586322 and b3 = 0.829181. Use full precision in the supplied code; rounding before matching can change matches near a caliper boundary.

Logistic regression is convenient, but main effects may miss nonlinear selection or interactions. Sparse categories, separation, measurement error and small samples can cause further problems. Consider justified nonlinear terms or alternative estimators, and assess their resulting balance without selecting models to obtain a desired earnings effect. This is a different use of logistic regression from the outcome interpretation covered in the logistic regression results guide.

Classification accuracy, AUC and treatment-model p-values are not the main matching-quality criteria. Perfectly distinguishing the groups may indicate that useful comparison is difficult. A model with good prediction can still leave substantial covariate imbalance, while a less discriminating model may produce adequate comparisons. Balance and support answer the design question.

Specify the matching algorithm completely

Nearest-neighbour matching chooses comparison adults using a stated distance. For one-to-one matching, each retained treated adult receives one comparison. A larger fixed ratio can use more comparison data but may require more distant matches. With variable ratios, weights must ensure that treated adults do not receive different influence merely because their sets contain different numbers of controls.

Without replacement, a comparison adult can enter only one matched set. The order matters because adults compete for comparisons. With replacement, a suitable control can serve several treated adults; this can improve closeness but requires multiplicity weights and uncertainty methods accounting for repeated individuals and matched sets. Repeated controls are not independent new people.

A caliper limits the permitted distance. Probability-scale and logit-scale distances are different. Austin's caliper simulations support a commonly used starting point of 0.2 standard deviations of the logit score in studied settings; this is not a universal optimum or a guarantee of balance. Report the scale and exactly which standard deviation you used.

Our selected design uses one-to-one nearest-neighbour matching without replacement, with the closest available pair selected first. Specifically:

  1. Compute each adult's fitted logit score, using the complete eligible sample.

  2. Compute its ordinary sample standard deviation across all eligible adults.

  3. List all treated-control pairs whose absolute logit difference is at most 0.2 times that standard deviation.

  4. Sort by increasing distance, then by treated ID and control ID to break exact ties.

  5. Traverse that list, accepting a pair only when neither adult has already been matched. Stop when no further eligible pair remains.

This is greedy matching, not an optimization of the total distance or number retained. An early close pair can prevent another person from finding a match. It does not require every covariate to be close within every pair. The official MatchIt nearest-neighbour documentation describes matching order, replacement and calipers; the hand-coded implementation below fixes every rule explicitly.

Worked example: track retention and calculate balance

The generator creates 480 synthetic adults: 171 enrollees and 309 nonparticipants. There are no missing values. This is a newly generated teaching dataset, not the commonly used Lalonde training dataset.

The fitted logit-score standard deviation is 0.605323, giving a raw logit caliper of 0.2 × 0.605323 = 0.121065. No separate range-trimming rule is applied. Before matching, control scores range from 0.086131 to 0.712315 and treated scores from 0.116054 to 0.686854. That overlap makes matching possible, but says little by itself about balance or local comparison density.

Sample flow under the selected closest-first matching design
GroupEligible before matchingRetainedNot retained
Treated adults17115714
Comparison adults309157152
Total adults480314166

The result is 157 disjoint pairs. The 14 unmatched treated adults are excluded because the algorithm cannot allocate an eligible unused control; this does not imply that every excluded person lies outside the original score ranges. The comparison no longer targets all 171 enrollees. Describe the retained adults and compare their baseline profile with the excluded enrollees before generalizing.

Calculate standardized mean differences with a fixed denominator

For each continuous covariate, this example uses SMD = (treated mean - control mean) / original treated-group SD. The denominator is the sample standard deviation among all eligible treated adults before matching, held fixed for the before and after calculations. Pooled and other denominators also exist; name the convention and use it consistently. The cobalt documentation explains these choices and why the same denominator should be retained.

Baseline balance before and after matching, with signed SMDs
CovariateOriginal treated SDBefore treated meanBefore control meanBefore SMDAfter treated meanAfter control meanAfter SMD
Age, years10.49729839.08187135.9385110.29944538.45222938.3057320.013956
Prior employment, months6.81890713.53216411.3074430.32625813.25477713.751592-0.072858
Baseline earnings, CU456.4958521050.959064897.0064720.3372491014.859873988.4777070.057793

For example, the post-match age calculation is (38.452229 - 38.305732) / 10.497298 = 0.013956. Displayed inputs are rounded; the code computes with full precision. Negative SMDs mean that the treated mean is lower.

All three absolute post-match SMDs are below 0.1, a common screening threshold rather than proof of negligible bias. Examine distributions, variance ratios, tails and substantively important interactions as well; equal means can conceal different distributions. For binary covariates, specify whether you report standardized differences or raw differences in proportions. Software defaults differ. Avoid using nonsignificant baseline tests as evidence of balance: their results depend heavily on sample size.

A Love plot places covariates on one axis and their before/after absolute SMDs on the other. A reference line at 0.1 is an aid to interpretation. Show labels, the denominator convention and all prespecified covariates. The R code provides that plot and score histograms; no executed R graphics or distributional diagnostic results are claimed here.

Design development also matters. An initial descending-score order retained 166 pairs but left absolute employment and earnings SMDs of 0.138700 and 0.124455. The selected closest-first order improves those mean-balance checks at the cost of retaining fewer adults. This decision uses covariate balance and retention, not the preferred earnings estimate. Keep such decisions in the analysis log, ideally while outcome comparisons are masked.

Estimate the matched contrast and respect its uncertainty

With one treated and one distinct control in each pair, give every pair equal weight. The mean within-pair difference equals the difference between the matched group means. For variable ratios or replacement, that simplification needs the correct matching weights.

The matched treated mean is 1290.211270 CU and the matched control mean is 1102.968524 CU. The estimated contrast is 1290.211270 - 1102.968524 = 187.242747 CU per month. This is an estimator of the retained-treated average effect only under the stated identification assumptions; otherwise it is an adjusted observational comparison. The unmatched group difference was 326.920890 CU, but its reduction does not measure the amount of confounding removed.

An explicitly limited working interval

For this continuous-outcome, disjoint-pair illustration, let d be the vector of within-pair earnings differences. Under a working model treating pair differences as independent observations from the relevant target distribution, use SE = SD(d) / sqrt(number of pairs). This accounts for the paired comparison through the differences; treating all matched rows as an independent two-sample comparison would discard that structure.

Here the sample SD of differences is 367.854741 CU, so the paired working SE is 367.854741 / sqrt(157) = 29.358004 CU. A conventional approximate 95% normal interval, estimate ± 1.96 × SE, is 129.701058 to 244.784435 CU. Both implementations independently reproduce these calculations.

This working interval is conditional on the selected matched comparison. It does not separately propagate propensity-model fitting, design selection or changing match membership. Matching without replacement draws controls from a shared reservoir; independence of pair differences is a working approximation, not a consequence of merely assigning pair IDs. The deterministic teaching data provide no empirical demonstration of repeated-sampling coverage. The interval also excludes bias from omitted confounders, model misspecification and remaining imbalance. Do not present it as a validated population causal confidence interval or proof that training works.

For a real dissertation, choose and justify inference for the actual estimator, sampling design, weighting, original clusters and matched structure. Outcome models with suitable matched-set cluster-robust covariance are one approach discussed in the MatchIt effects guide. With reused controls, both repeated-person and matched-set dependence require attention. A generic paired formula is not sufficient. General interval interpretation is covered in the confidence intervals guide.

Do not assume an ordinary row-resampling bootstrap solves the problem. Abadie and Imbens (2008) establish bootstrap failure for fixed-neighbour matching with replacement under their conditions. That result is not a claim that every matched-set bootstrap or every matching estimator is invalid; justify the particular procedure you use.

Reproduce the data and calculations in R

Execution status: R code unexecuted. Python and JavaScript independently regenerated every row, fitted the logistic model, selected exactly the same pairs and verified the reported values. The explicit integer generator avoids relying on identical random-number generators across languages. It is a reproducibility device, not a realistic model of a labour market.

Run the blocks in order in one R session. Base R is sufficient for the numerical example. The final optional block needs MatchIt and cobalt already installed. Record sessionInfo() and package versions in your own dissertation appendix. If a reproduced result differs, inspect inputs and full-precision distances before interpreting it.

# All data are synthetic. This R code has not been executed.
state <- 83026
next_u <- function() {
  state <<- (16807 * state) %% 2147483647
  state / 2147483647
}
u <- matrix(replicate(480 * 5, next_u()), ncol = 5, byrow = TRUE)
d <- data.frame(
  id = seq_len(480),
  age = 20 + floor(36 * u[, 1]),
  months = floor(25 * u[, 2]),
  baseline = 200 + floor(1601 * u[, 3])
)
true_eta <- with(d, -0.55 + 0.025 * (age - 38) +
  0.055 * (months - 12) + 0.00055 * (baseline - 1000))
d$treat <- as.integer(u[, 4] < plogis(true_eta))
d$outcome <- with(d, 250 + 0.70 * baseline + 12 * months +
  3 * (age - 38) + 180 * treat + 500 * (u[, 5] - 0.5))
d$age10 <- (d$age - 38) / 10
d$work12 <- (d$months - 12) / 12
d$earn1000 <- (d$baseline - 1000) / 1000
fit <- glm(treat ~ age10 + work12 + earn1000, data = d,
  family = binomial(), control = glm.control(epsilon = 1e-12))
stopifnot(fit$converged)
eta <- predict(fit, type = "link")
ps <- plogis(eta)
coef(fit)

make_pairs <- function(multiplier) {
  edges <- expand.grid(i = which(d$treat == 1),
    j = which(d$treat == 0))
  edges$distance <- abs(eta[edges$i] - eta[edges$j])
  edges <- edges[edges$distance <= multiplier * sd(eta), ]
  edges <- edges[order(edges$distance, edges$i, edges$j), ]
  used <- rep(FALSE, nrow(d))
  chosen <- logical(nrow(edges))
  for (k in seq_len(nrow(edges))) {
    i <- edges$i[k]; j <- edges$j[k]
    if (!used[i] && !used[j]) {
      chosen[k] <- TRUE
      used[c(i, j)] <- TRUE
    }
  }
  edges[chosen, , drop = FALSE]
}
pairs <- make_pairs(0.2)
stopifnot(!anyDuplicated(c(pairs$i, pairs$j)))

balance <- function(p) {
  variables <- c("age", "months", "baseline")
  result <- t(vapply(variables, function(v) {
    x <- d[[v]]
    original_sd <- sd(x[d$treat == 1])
    before_t <- mean(x[d$treat == 1])
    before_c <- mean(x[d$treat == 0])
    after_t <- mean(x[p$i]); after_c <- mean(x[p$j])
    c(originalSD = original_sd, beforeT = before_t,
      beforeC = before_c, beforeSMD = (before_t - before_c)/original_sd,
      afterT = after_t, afterC = after_c,
      afterSMD = (after_t - after_c)/original_sd)
  }, numeric(7)))
  result
}
effect <- function(p) {
  differences <- d$outcome[p$i] - d$outcome[p$j]
  estimate <- mean(differences)
  se <- sd(differences) / sqrt(length(differences))
  c(pairs = length(differences), estimate = estimate,
    differenceSD = sd(differences), workingSE = se,
    lower = estimate - 1.96 * se, upper = estimate + 1.96 * se)
}
balance(pairs)
effect(pairs)
lapply(c(0.1, 0.2, 0.3), function(c) {
  p <- make_pairs(c)
  list(caliperMultiplier = c, effect = effect(p), balance = balance(p))
})
write.csv(d, "harbour-synthetic-adults.csv", row.names = FALSE)
write.csv(pairs, "harbour-matched-pairs.csv", row.names = FALSE)
sessionInfo()

The generator inserts a known constant increment of 180 CU for treatment. That construction is available only because this is synthetic data. It does not force the matched estimate to equal 180: different adults still have different baseline attributes and noise. Real datasets do not disclose both potential outcomes.

Optional package cross-check and diagnostic plots

The numerical results above come from the explicit algorithm, not an executed MatchIt run. The call below expresses the same closest-first design with a supplied logit-distance vector and a raw-unit caliper. std.caliper = FALSE prevents a second standardization. Check pair IDs and balance against the explicit implementation; do not silently substitute a different package result.

# Optional; install these packages separately if needed.
m <- MatchIt::matchit(treat ~ age + months + baseline, data = d,
  method = "nearest", distance = eta, estimand = "ATT",
  ratio = 1, replace = FALSE, m.order = "closest",
  caliper = 0.2 * sd(eta), std.caliper = FALSE, discard = "none")
packageVersion("MatchIt")
packageVersion("cobalt")
cobalt::bal.tab(m, un = TRUE, s.d.denom = "treated", binary = "std")
cobalt::love.plot(m, abs = TRUE, thresholds = c(m = 0.1),
  s.d.denom = "treated", binary = "std", drop.distance = TRUE)

# Histograms of probabilities, not the logit-distance vector.
retained <- c(pairs$i, pairs$j)
breaks <- seq(0, 1, by = 0.05)
par(mfrow = c(2, 2))
for (label in c("Before", "After")) {
  idx <- if (label == "Before") seq_len(nrow(d)) else retained
  for (g in c(0, 1)) {
    hist(ps[idx[d$treat[idx] == g]], breaks = breaks,
      xlim = c(0, 1), freq = FALSE,
      main = paste(label, "treatment =", g),
      xlab = "Estimated probability of enrolment")
  }
}
par(mfrow = c(1, 1))

If asking MatchIt to estimate the scores directly instead, its documented distance = "glm", link = "linear.logit" option requests the linear predictor. Merely requesting link = "logit" returns probabilities for the distance. The official distance documentation explains the distinction. The all-sample SD convention here is explicit; do not assume it equals every package's standardized-caliper default.

Check design sensitivity and unmeasured confounding

The same data, fitted scores, order and replacement rule give the following alternative calipers. Only the caliper multiplier changes.

Caliper sensitivity using closest-first matching on the same synthetic adults
Logit-SD multiplierRetained pairsMean earnings contrast, CULargest absolute post-match SMD
0.1154188.1850410.066660
0.2, selected design157187.2427470.072858
0.3159188.2372780.074709

The contrasts are similar in this exercise, but the retained adults differ. These are comparisons of changed designs and targets, not interchangeable estimates of exactly the same population effect. Document all substantively justified design checks, including disappointing ones. Avoid selecting the specification with the smallest p-value.

Hidden confounding requires a separate analysis. Suppose unmeasured reliable transport were more common among matched enrollees, independently predicting higher earnings. Under a deliberately simplified additive bias model, a prevalence difference of 0.20 and an earnings association of 300 CU would create 0.20 × 300 = 60 CU of bias. Subtracting that assumed bias gives 187.242747 - 60 = 127.242747 CU. Those inputs are hypothetical, not estimated from these records, and this arithmetic does not constitute a validated sensitivity analysis or produce an adjusted confidence interval.

For a formal matched-study analysis, Rosenbaum's sensitivity framework examines conclusions under bounded hidden differences in treatment-assignment odds. Gamma equal to one corresponds to no hidden assignment-odds difference under that model; larger Gamma allows greater departure. Gamma is an odds ratio bound, not a correlation or an earnings effect. Choose the test and sensitivity method for the actual matched design and outcome. No Rosenbaum bounds, critical Gamma or hidden-confounding p-values were computed here. Good observed balance does not establish that hidden bias is small.

Report the methodology and results transparently

Your methods section should identify eligibility and time zero, enrolment coding, follow-up, the initial estimand, baseline covariate rationale, missing-data handling, propensity-model formula, distance scale, caliper SD convention, matching ratio, replacement, ordering and tie rule. State whether support restrictions or rematching were applied and retain an ID-level match log.

Your results should show sample flow, original and matched balance, the profiles of retained and excluded treated adults, score distributions, the final target and the effect with a justified uncertainty procedure. Distinguish diagnostics actually performed from recommended future checks. Explain residual confounding, selection, generalizability and whether the comparison supports a causal interpretation. The statistical reporting guide covers broader presentation conventions; the paragraphs below add matching-specific information.

Model methods paragraph

In this synthetic cohort, treatment was voluntary programme enrolment at a common baseline and the outcome was monthly earnings twelve months later. We estimated enrolment probabilities by logistic regression using baseline age, prior employment months and baseline earnings, specified as scaled linear main effects. We selected disjoint nearest-neighbour pairs without replacement in increasing absolute logit-distance order, breaking ties by treated and control IDs. The caliper was 0.2 times the all-eligible-sample logit-score SD, with no separate range trimming. We assessed signed SMDs using the original treated-group SD for each covariate as the fixed denominator. Matching decisions considered covariate balance and retention. We estimated the equal-weight mean of within-pair earnings differences and an explicitly conditional normal working interval from their sample SD.

Model results and limitations paragraph

Matching retained 157 of 171 treated adults and 157 of 309 potential controls, narrowing the target to retained treated adults. The largest absolute SMD among the three specified baseline covariates fell from 0.337 to 0.073. Their matched mean monthly earnings contrast was 187.24 CU, with a paired working SE of 29.36 CU and an approximate conditional 95% normal interval of 129.70 to 244.78 CU. This illustrative interval treats pair differences as independent and does not separately propagate score estimation, match selection or design development. Full distributional balance and formal hidden-bias sensitivity were not established. The observational comparison requires untestable identification assumptions and cannot establish programme effectiveness; the data and results are entirely synthetic.

Common PSM mistakes to avoid

  • Treating a propensity score as the probability of a successful outcome.

  • Selecting covariates by treatment-model significance alone, or adding post-treatment variables.

  • Reporting only treatment prediction accuracy or score overlap instead of baseline covariate balance.

  • Writing “caliper 0.2” without its distance scale and standardization convention.

  • Hiding matching order, excluded treated adults or changed target populations.

  • Applying ordinary independent-row uncertainty to reused controls or ignoring original site-level clustering.

  • Presenting an earnings contrast as causal simply because matched SMDs meet a threshold.

  • Trying designs until the preferred outcome result appears.

Frequently asked questions

Does matching make my study experimental?

No. Treatment was still chosen through an observational process. Matching addresses recorded characteristics; the absence of important unmeasured confounding remains an assumption, even when the observed balance looks good.

Should I match on every available baseline variable?

No. Use the causal structure, measurement timing and subject knowledge. Genuine confounders and strong baseline outcome predictors deserve consideration; colliders and treatment consequences can introduce bias. More columns do not automatically produce a more credible design.

Is a caliper of 0.2 always correct?

No. It is a common starting multiplier on a specified standard deviation, often applied to logit scores. Probability-scale and logit-scale calipers differ. Evaluate justified alternatives using balance, retention and the target rather than assuming a single rule suits every study.

Must I keep all treated participants?

Do not force poor matches merely to retain them. Explain why some are unmatched and describe whose effect remains targeted. Dropping treated adults can improve comparability while limiting generalizability; it does not preserve an unrestricted ATT by changing its label.

Can I run a regression after matching?

Yes. An appropriate outcome model can address residual imbalance or improve precision, using matching weights and an uncertainty method suited to the matched and original sampling structure. Regression does not excuse poor overlap or identify an unmeasured confounder. Explain whether your resulting estimate is marginal for the retained target or conditional on model covariates.

What if my groups are still unbalanced?

Revisit the measured covariate set, functional forms, matching distance and substantive eligibility restrictions while keeping outcome comparisons masked. Consider another design or acknowledge that the available data do not support the planned effect comparison. Do not suppress the failed balance table.

Is the confidence interval here ready to copy into my dissertation?

No. It is a reproducible working calculation for synthetic disjoint pairs under stated assumptions. Your estimator may involve different ratios, reused controls, clusters or target selection. Justify inference for those conditions and report its limits. R and the optional package workflow were not executed here.

Is caliper sensitivity the same as unmeasured-confounding sensitivity?

No. Changing calipers checks dependence on an observed-data design choice and can change the retained target. Hidden-bias sensitivity evaluates additional assumptions about an unrecorded selection process. Neither demonstrates that all confounding has been removed.

Support for a transparent dissertation analysis

If you need help understanding an estimand, checking your matching specification or explaining diagnostics, Acadelyra's academic support services can support your own analysis and writing. Keep research decisions and authorship with you, follow your institution's rules on external assistance and acknowledgement, and do not treat academic support as a guarantee of statistical significance or a causal finding.

References and further reading