{
  "id": "difference-in-differences",
  "title": "Difference-in-Differences",
  "lang": "en",
  "source_lang": "en",
  "summary": "Difference-in-differences estimates causal effects by comparing outcome changes across treated and comparison groups under assumptions about their untreated trends.",
  "category": "mathematics",
  "subcategory": "probability-statistics",
  "type": "concept",
  "aliases": [
    "DiD",
    "DID",
    "DD",
    "double-difference estimator",
    "differences-in-differences"
  ],
  "generated_at": "2026-11-03",
  "model": "pro/gpt-6.1-sol",
  "url": "https://aiwiki.page/en/difference-in-differences/",
  "translations": {
    "zh-Hans": {
      "url": "https://aiwiki.page/zh/difference-in-differences/",
      "json": "https://aiwiki.page/zh/difference-in-differences.json"
    }
  },
  "sections": [
    {
      "heading": "",
      "text": "Difference-in-differences is a statistical research design that estimates the effect of an intervention by comparing changes in outcomes for an exposed group with changes for a comparison group. It is widely used in econometrics, public health, and other fields where researchers observe policy changes or institutional interventions but cannot randomly assign exposure. Its distinguishing feature is that neither a before-and-after comparison within the treated group nor a contemporaneous comparison between groups is sufficient: the estimator subtracts one change from the other.\n\nThe central identification assumption is that, without the intervention, the groups would have experienced the same average change in outcomes. This parallel-trends assumption permits groups to differ permanently in their outcome levels, while excluding untreated changes that would systematically favor one group over the other. Under appropriate additional conditions, the resulting difference identifies an average causal effect for the treated population.\n\nThe familiar two-group, two-period calculation extends to longitudinal data, repeated cross-sectional surveys, multiple treatment dates, and dynamic effects. These extensions require careful distinctions between the causal quantity of interest and the coefficient produced by a particular regression. Modern research has especially emphasized heterogeneous treatment effects, the limitations of conventional fixed-effects regressions, and valid uncertainty estimates when policy exposure is shared across many observations."
    },
    {
      "heading": "Historical development and empirical uses",
      "text": "Difference-in-differences belongs to the broader tradition of learning from natural experiments: circumstances in which institutions or events generate exposure differences that can support causal comparisons. It is not defined by a particular estimation algorithm. Its essential logic is a comparison of changes, and examples of that logic predate the terminology and regression methods now associated with it.\n\nJohn Snow’s investigation of London cholera in the 1850s is frequently discussed as an early antecedent. Different water companies supplied households in overlapping areas, and the Lambeth company moved its intake upstream of major sources of sewage contamination. Comparisons involving water suppliers, mortality, and changing exposure helped distinguish competing explanations of cholera transmission. Snow’s work was not a single modern difference-in-differences specification, but it illustrates the importance of constructing a comparison that separates an exposure change from pre-existing differences between populations.\n\nA prominent modern application was David Card and Alan Krueger’s 1994 study of fast-food employment. New Jersey increased its minimum wage from $4.25 to $5.05 per hour in April 1992, while neighboring Pennsylvania did not make the same change. The researchers compared employment changes at surveyed restaurants across the two states. Their original survey covered 410 restaurants. The study became influential both for its substantive findings and for making a transparent policy comparison central to empirical labor-market research. Subsequent analyses using different data also illustrated how measurement and sample construction can affect estimates from the same broad design.\n\nDifference-in-differences is now applied to changes in taxation, school funding, environmental regulation, insurance eligibility, transportation access, and many other interventions. A policy may vary across states, municipalities, firms, schools, or individuals. The unit receiving treatment need not be the unit at which outcomes are measured: a state law can affect thousands of individual observations, while still providing only one state-level treatment assignment.\n\nSeveral methodological developments changed how these applications are evaluated. Marianne Bertrand, Esther Duflo, and Sendhil Mullainathan’s 2004 analysis drew attention to serial correlation and understated uncertainty in conventional applications. Research published around 2020–2021 by Andrew Goodman-Bacon, Brantly Callaway and Pedro Sant’Anna, and Liyang Sun and Sarah Abraham clarified problems arising when treatment begins at different dates and effects vary across groups or over time. These contributions shifted attention from simply including fixed effects to specifying which comparisons identify which causal effects."
    },
    {
      "heading": "The two-group, two-period design",
      "text": "Consider units observed before and after an intervention. Let \\(D_i=1\\) indicate membership in the treated group and \\(D_i=0\\) membership in the comparison group. Let \\(t=0\\) denote the pre-intervention period and \\(t=1\\) the post-intervention period. Writing \\(\\bar Y_{d,t}\\) for an observed group-period mean, the sample difference-in-differences estimator is\n\n\\[\\widehat{\\tau}_{\\mathrm{DiD}} = (\\bar Y_{1,1}-\\bar Y_{1,0}) - (\\bar Y_{0,1}-\\bar Y_{0,0}).\\]\n\nSuppose average employment at treated establishments increases from 20 to 23 workers, while comparison establishments increase from 15 to 16. The treated group gains three workers, but one worker of that increase is attributed to the change also observed in the comparison group. The estimate is therefore \\(3-1=2\\) workers per establishment. The calculation does not claim that the initial five-worker difference was caused by treatment.\n\nThe causal interpretation is expressed through potential outcomes. Let \\(Y_{it}(1)\\) denote the outcome unit \\(i\\) would have at time \\(t\\) under treatment and \\(Y_{it}(0)\\) the outcome without treatment. In the standard design, treatment occurs only for the treated group in the post-intervention period. The target is the average treatment effect on the treated, or ATT:\n\n\\[\\tau_{\\mathrm{ATT}} = E[Y_{i1}(1)-Y_{i1}(0)\\mid D_i=1].\\]\n\nThe first term is observed for treated units after intervention; the second is counterfactual. Difference-in-differences reconstructs its mean by adding the comparison group’s observed change to the treated group’s pre-intervention mean:\n\n\\[E[Y_{i1}(0)\\mid D_i=1] = E[Y_{i0}(0)\\mid D_i=1] + E[Y_{i1}(0)-Y_{i0}(0)\\mid D_i=0].\\]\n\nThis equality is justified by parallel trends, not by an algebraic identity. Subtracting the constructed untreated outcome from the observed treated outcome yields the population version of the double difference. Expectations here refer to the population means relevant to the study; their sample analogues introduce sampling uncertainty.\n\nThe design therefore removes two distinct sources of differences: time-invariant group differences and time changes common to both groups. It does not automatically remove group-specific shocks. If treated establishments would have gained two additional workers because of an unrelated local expansion, the double difference would combine that expansion with the policy effect.\n\nThe ATT is also distinct from an average effect for everyone. Even a valid estimate for establishments exposed to a particular policy does not establish what the same policy would do in another region, at another date, or under a different implementation. Identification within the studied setting and generalization beyond it are separate questions."
    },
    {
      "heading": "Identification assumptions and their meaning",
      "text": "The defining assumption is equality of average untreated changes:\n\n\\[E[Y_{i1}(0)-Y_{i0}(0)\\mid D_i=1] = E[Y_{i1}(0)-Y_{i0}(0)\\mid D_i=0].\\]\n\nThis is a restriction on unobserved counterfactual outcomes after treatment. It is not a requirement that observed outcomes remain parallel once treatment begins; a treatment effect can make those paths diverge. Nor does it require equal initial outcomes. A persistently higher employment level in one region is compatible with parallel trends.\n\nParallel trends is weaker than requiring treatment assignment to be unrelated to every determinant of outcomes, but it remains a substantive restriction. Selection into treatment based on a permanent characteristic can be compatible with the design. Selection based on an impending outcome change generally is not. For example, a government may introduce assistance specifically where closures are expected to accelerate. A comparison with regions lacking that impending decline then contains confounding even if both groups looked similar in earlier years.\n\nNo anticipation requires that future treatment not affect outcomes used as untreated observations. If firms adjust staffing when a law is announced rather than when it takes effect, observations between announcement and implementation may already be affected. In the two-period framework, the usual requirement is that the treated group’s pre-period outcome equals its untreated potential outcome. In longer panels, plausible anticipation changes which observations and comparison groups qualify as untreated.\n\nThe standard formulation also assumes a sufficiently well-defined intervention and no relevant interference between units. If a treated municipality attracts customers away from neighboring comparison municipalities, their outcomes no longer represent what would happen without exposure to the intervention. Such spillovers may make the estimated contrast larger or smaller than the direct effect. A common national policy operating in the background is not itself disqualifying if its relevant consequences are shared, but differential exposure to it may be.\n\nParallel trends can instead be imposed conditional on pre-treatment characteristics \\(X_i\\):\n\n\\[E[\\Delta Y_i(0)\\mid D_i=1,X_i=x] = E[\\Delta Y_i(0)\\mid D_i=0,X_i=x].\\]\n\nThis formulation requires suitable overlap: treated units must have comparable untreated observations at relevant values of \\(X_i\\). The untreated changes are then averaged over the treated population’s covariate distribution. Conditional and unconditional parallel trends are different assumptions; adding covariates does not automatically strengthen a design.\n\nThese conditions provide statistical identification, not merely an estimation recipe. A precisely estimated coefficient can remain causally misleading when they fail. Conversely, treatment need not be randomly assigned for the assumptions to hold: the relevant issue is how assignment relates to untreated outcome changes."
    },
    {
      "heading": "Regression estimation and data structure",
      "text": "In the simplest design, difference-in-differences can be estimated using linear regression:\n\n\\[Y_{it} = \\alpha+\\gamma D_i+\\lambda P_t +\\tau(D_iP_t)+\\varepsilon_{it},\\]\n\nwhere \\(P_t\\) indicates the post-intervention period. With an intercept, the two main effects, and their interaction, ordinary least squares reproduces the difference between the four unweighted cell means, provided each cell is observed and the regression is unweighted. The coefficient \\(\\tau\\) is the double difference; the regression itself supplies no additional causal justification.\n\nFor panel data, where the same units are followed over time, a common specification is\n\n\\[Y_{it}=\\alpha_i+\\lambda_t+\\tau A_{it}+\\varepsilon_{it}.\\]\n\nHere \\(\\alpha_i\\) are unit effects, \\(\\lambda_t\\) are period effects, and \\(A_{it}\\) records treatment exposure. A fixed-effects model absorbs all time-invariant unit characteristics, including unmeasured ones, and time effects absorb shocks shared across units. With two periods and common treatment timing, differencing eliminates \\(\\alpha_i\\), leaving a comparison of outcome changes. With many periods and varying treatment dates, the same-looking regression can have a much less direct interpretation.\n\nDifference-in-differences also works with repeated cross-sections, in which different people or establishments are sampled at each date. The design then compares population means rather than individual changes. Its interpretation depends on a stable target population or an explicit treatment of changing composition. A rise in average wages, for example, may reflect wage increases for continuing workers, the departure of low-wage workers, or both. Those are different outcomes, even though they can produce the same group-level mean.\n\nCovariate-adjusted estimation can use outcome regression, weighting, or combinations of the two. Propensity-score weighting uses estimated treatment probabilities to make untreated observations resemble the treated population in pre-treatment characteristics. Doubly robust estimators combine a model for untreated outcome changes with a treatment-probability model; under their stated conditions, consistency can hold when either one of these nuisance models is correctly specified. This robustness does not protect against failure of the identifying parallel-trends assumption.\n\nOutcome scale is consequential. Parallel trends in levels means equal expected absolute changes; parallel trends in logarithms corresponds to a different restriction involving changes in log outcomes. Neither implies the other. A coefficient from a log-outcome regression is a contrast of mean logarithms and is not automatically the percentage ATT in outcome levels. For binary outcomes, a linear model estimates a probability-scale contrast, whereas an interaction in logistic regression is on the log-odds scale and generally does not equal a difference-in-differences in probabilities. Choice of scale is therefore part of the causal specification, not simply a cosmetic transformation."
    },
    {
      "heading": "Event studies and dynamic treatment effects",
      "text": "An event study organizes observations by time relative to treatment. If unit \\(i\\) first receives treatment in period \\(G_i\\), its event time is \\(k=t-G_i\\). Negative values refer to periods before treatment, zero to the adoption period, and positive values to periods afterward. This arrangement distinguishes immediate effects from effects that accumulate, fade, or emerge only after a delay.\n\nA conventional regression takes the form\n\n\\[Y_{it} = \\alpha_i+\\lambda_t+ \\sum_{k\\ne -1}\\beta_k \\mathbf{1}\\{t-G_i=k\\} +\\varepsilon_{it},\\]\n\nwith event time \\(-1\\) omitted as the reference period. The symbol \\(\\mathbf{1}\\) is an indicator function. The exact specification must define how never-treated units enter, which event times are included, and whether distant periods are combined into endpoint categories. When treatment timing is common and appropriate controls are available, the coefficients describe changes relative to the baseline difference between groups.\n\nPost-treatment coefficients can reveal mechanisms obscured by a single average. A training program might initially reduce earnings while participants attend courses and increase them later. An infrastructure project may produce disruption during construction before delivering benefits after opening. A single treatment coefficient averages these phases in a way that depends on the observed periods and regression weights. Moreover, an annual coefficient for the adoption year may mix treated and untreated months if implementation occurs partway through the year.\n\nPre-treatment coefficients are commonly used to assess whether observed trends contradict the design. A systematic divergence before exposure can indicate different untreated trajectories, anticipation, or an incorrectly dated intervention. Nevertheless, a statistically insignificant pre-trend does not establish parallel trends. Tests may have low statistical power, especially with few pre-treatment periods or noisy outcomes, and equality in earlier periods does not logically guarantee equality after treatment.\n\nEvent-study graphs also require uncertainty statements suited to their purpose. A collection of pointwise intervals does not provide the same protection as a simultaneous confidence band for the entire path. Testing many leads separately introduces multiple-testing concerns. Selecting a specification only because its leads are insignificant can distort subsequent inference.\n\nWhen adoption dates differ, conventional event-time coefficients may mix effects across cohorts and event times rather than isolate the displayed horizon. In particular, already-treated units can implicitly act as controls for newly treated units. Modern event studies therefore often estimate cohort-specific effects first and aggregate them afterward. The set of cohorts observed at long horizons also matters: apparent changes in the dynamic profile can reflect changing cohort composition rather than changes in any cohort’s treatment effect."
    },
    {
      "heading": "Staggered adoption and heterogeneous effects",
      "text": "In staggered-adoption designs, different groups begin treatment at different dates. Examples include jurisdictions introducing a policy in successive years or firms adopting a technology at different times. In the common absorbing-treatment case, a unit remains treated after adoption. Such data contain many possible comparisons, but those comparisons do not necessarily identify the same causal quantity.\n\nA useful building block is the group-time average treatment effect,\n\n\\[\\operatorname{ATT}(g,t) = E[Y_{it}(1)-Y_{it}(0)\\mid G_i=g], \\qquad t\\ge g,\\]\n\nwhere \\(g\\) denotes the first treatment period. The notation \\(Y_{it}(1)\\) here represents the outcome under the treatment history beginning at \\(g\\), not merely an isolated one-period exposure. Each group-time effect asks what treatment did to a particular adoption cohort at a particular calendar date.\n\nUnder cohort-specific parallel trends and no anticipation, these effects can be identified by comparing that cohort’s change with changes among never-treated units or units not yet treated. For example, the effect on a cohort adopting in 2015, measured in 2017, can use units whose adoption is later than 2017, provided their outcomes have not already responded in anticipation. The same units cease to be valid untreated comparisons once their exposure or anticipation period begins.\n\nA conventional two-way fixed-effects regression does not automatically respect this distinction. Goodman-Bacon’s decomposition shows that, in a standard balanced-panel setting, the treatment coefficient can be expressed as a weighted average of two-group, two-period comparisons. Some compare treated units with never-treated units; others compare earlier and later adopters. Comparisons using earlier adopters as controls after their treatment can subtract changes in their treatment effects from the effects of later adopters.\n\nTwo weighting statements must be distinguished. The weights on the constituent two-by-two estimators in the standard decomposition are nonnegative. However, when the overall regression coefficient is represented in terms of underlying heterogeneous group-time treatment effects, some effects can receive negative weights. Consequently, a regression coefficient can be difficult to interpret and may even have a sign opposite to the underlying effects. These issues arise from treatment-effect heterogeneity and changing exposure, not simply from imprecise estimation.\n\nCallaway and Sant’Anna’s group-time approach, Sun and Abraham’s cohort-interacted event study, and untreated-outcome imputation approaches address these problems in different ways. Their common emphasis is to define credible untreated comparisons and keep the causal estimand explicit. Estimated group-time effects can be aggregated by cohort size, event time, or calendar time, but these summaries answer different questions. After every unit is treated, effects for later periods generally lack contemporaneous untreated comparisons; identifying them requires additional restrictions rather than a routine extension of the same comparison."
    },
    {
      "heading": "Statistical inference and dependence",
      "text": "A difference-in-differences estimate is a statistic calculated from data, and its uncertainty depends on the sampling and assignment structure. Policy studies often contain many individual observations but relatively few independent policy units. Ten thousand workers observed within ten states do not generally provide the same information about a state-level policy as ten thousand independently treated workers.\n\nTwo dependence patterns are especially important. Outcomes can be correlated among units sharing a jurisdiction, and shocks within a jurisdiction can persist over time. Ignoring these patterns can produce standard errors that are too small and confidence intervals that are too narrow. Adding unit and time fixed effects does not remove all residual dependence. For example, a persistent state-specific economic shock may remain after common year effects and permanent state differences have been absorbed.\n\nCluster-robust inference allows residuals to be correlated within a cluster while relying on suitable independence or weak dependence across clusters. In many policy applications, the policy-assignment level is a natural clustering level. The cluster-robust covariance matrix for a regression has the general sandwich form\n\n\\[\\widehat{\\operatorname{Var}}(\\hat\\beta) = (X'X)^{-1} \\left( \\sum_{c=1}^{C}X_c'\\hat u_c\\hat u_c'X_c \\right) (X'X)^{-1},\\]\n\napart from finite-sample corrections. Here \\(c\\) indexes clusters, \\(X_c\\) is the cluster’s design matrix, and \\(\\hat u_c\\) is its vector of fitted residuals. The formula retains within-cluster residual products rather than treating every observation as independent.\n\nConventional cluster approximations can be unreliable with few clusters, highly unequal cluster sizes, or very few treated clusters. Small-sample corrections and wild cluster bootstrap procedures can improve inference in some settings, but no adjustment makes a design with one treated jurisdiction equivalent to a large experiment. Methods based on alternative treatment assignments require a defensible assignment mechanism or exchangeability assumption. A distribution generated by arbitrarily relabeling states is not automatically a valid randomization distribution.\n\nSpatial dependence can also extend beyond administrative boundaries. Neighboring regions may share shocks even when treatment is assigned separately. Depending on the setting, inference may require spatial covariance adjustments, multiple clustering dimensions, or a model of the dependence structure. The appropriate method follows the sources of variation and dependence, not merely the software default.\n\nStatistical uncertainty is separate from identification uncertainty. A narrow interval can describe the sampling precision of a biased comparison. Standard confidence intervals do not ordinarily account for possible violations of parallel trends, incorrect treatment dates, spillovers, or alternative outcome definitions. Those uncertainties require design analysis or explicitly expanded inferential procedures."
    },
    {
      "heading": "Diagnostics, sensitivity, and threats to validity",
      "text": "The most direct diagnostic evidence concerns untreated outcome histories and the institutional process that generated treatment. Plotting group means can reveal changes that a regression table conceals: an outcome decline beginning before adoption, a one-time measurement break, or a comparison group affected by a separate intervention. Both outcome levels and changes matter, although similar levels alone provide little evidence about future untreated trends.\n\nPlacebo exercises examine implications of the design where no effect is expected. A fictitious treatment date placed before the actual intervention can reveal pre-existing divergence. An outcome that should not respond to treatment can detect broader group-specific shocks. These exercises are informative only when the placebo implication is substantively justified. A policy affecting employment may also affect migration or household income, so those variables are not necessarily valid “unaffected” outcomes.\n\nChanging composition is a recurring threat. In panels, differential attrition can change which units remain observed. In repeated cross-sections, migration, establishment entry, or changing survey coverage can alter group means. Some composition changes are themselves treatment effects. For example, a policy may change who enters employment, making wages among employed workers a selected outcome. Conditioning on continued employment can then introduce selection bias rather than isolate a stable wage effect.\n\nTreatment selection after an unusually high or low outcome creates another problem. If assistance is triggered by a temporary earnings decline, subsequent recovery may partly represent regression to the mean. A comparison group selected without the same temporary shock need not share that recovery. Similarly, controlling for post-treatment variables such as policy-induced investment can block part of the effect or generate additional bias; more controls do not necessarily mean a more credible design.\n\nFormal sensitivity analysis replaces an all-or-nothing treatment of parallel trends with explicit restrictions on possible violations. One approach bounds post-treatment departures relative to deviations observed before treatment; another constrains how sharply untreated trends can change over time. Methods developed by Ashesh Rambachan and Jonathan Roth provide a framework for obtaining robust confidence sets under specified restrictions of this kind. The resulting range depends on the restrictions chosen and can be wider than conventional intervals.\n\nOutcome measurement also requires scrutiny. Changes in reporting incentives, administrative definitions, inflation adjustment, or geographic boundaries can mimic policy effects. Estimates can additionally be sensitive to a small number of influential jurisdictions or to the chosen pre-treatment baseline. These diagnostics do not mechanically certify or invalidate a study: their value lies in identifying which substantive assumptions the causal interpretation actually requires."
    },
    {
      "heading": "Extensions and relationships to other designs",
      "text": "Triple differences add a third comparison dimension. Suppose a policy applies in one region but only to a defined eligibility group. A triple-difference estimator subtracts the treated-versus-comparison-region double difference for ineligible units from the corresponding double difference for eligible units:\n\n\\[\\widehat{\\tau}_{\\mathrm{DDD}} = \\widehat{\\tau}_{\\mathrm{DiD,eligible}} - \\widehat{\\tau}_{\\mathrm{DiD,ineligible}}.\\]\n\nThis can remove region-specific shocks shared across eligibility groups. Its identifying restriction is that, without treatment, the eligible–ineligible outcome gap would change similarly across regions. It does not eliminate the need for parallel-trends reasoning, and effects on supposedly ineligible units can compromise the interpretation.\n\nSynthetic control constructs a weighted combination of comparison units to reproduce a treated unit’s pre-intervention characteristics and outcomes. It is particularly associated with interventions affecting one or a few aggregate units. Standard difference-in-differences permits a fixed level gap and focuses on comparable changes, whereas synthetic control emphasizes pre-treatment fit under its own identifying structure. Synthetic difference-in-differences combines unit and time weighting with a double-difference-style adjustment. None of these methods turns a good pre-treatment fit into a guarantee about the untreated future.\n\nDifference-in-differences can also be combined with instrumental variables when a policy changes treatment receipt without determining it perfectly. The reduced-form outcome effect measures the effect of the policy-induced assignment or eligibility change. Dividing it by an appropriate first-stage effect on treatment receipt can identify a local treatment effect only under further conditions, including an exclusion restriction and suitable assumptions about compliance. The interpretation is not automatically the average effect of treatment for all exposed individuals.\n\nWith continuous treatment, such as a tax rate or subsidy amount, the meaning of the target becomes more complex. Parallel trends may identify effects relative to zero exposure for particular dose groups, while a causal comparison between two positive doses can require additional assumptions about selection into dose. A linear regression coefficient on treatment intensity imposes a particular summary structure and does not automatically represent a universal causal response to one extra unit of exposure.\n\nTreatment reversals and repeated interventions require attention to exposure histories. If an effect persists after a program ends, a formerly treated unit is not equivalent to a never-treated control. Event definitions must distinguish initiation, duration, cessation, and carryover. Similarly, neighboring-unit spillovers may require defining both own treatment and exposure to others’ treatment, producing direct and indirect effects rather than one undifferentiated coefficient.\n\nThe relationship to randomized experiments is therefore one of complementary design principles. Randomization can justify comparisons through the assignment mechanism; observational difference-in-differences instead relies on restrictions on untreated changes and exposure. Pre-treatment measurements can improve precision in either setting, but their presence alone does not create the same source of causal identification."
    }
  ],
  "links": [
    "econometrics",
    "public-health",
    "natural-experiment",
    "labor-market",
    "taxation",
    "expected-value",
    "confounding",
    "statistical-identification",
    "linear-regression",
    "statistical-interaction",
    "ordinary-least-squares",
    "fixed-effects-model",
    "propensity-score",
    "logistic-regression",
    "indicator-function",
    "statistical-power",
    "multiple-testing",
    "estimator",
    "standard-error",
    "confidence-interval",
    "covariance-matrix",
    "selection-bias",
    "regression-to-the-mean",
    "sensitivity-analysis",
    "instrumental-variables",
    "randomized-controlled-trial"
  ],
  "sources": [],
  "license": "https://creativecommons.org/licenses/by/4.0/"
}