% ---------------------------------------------------------------
%  Empirical strategy: Callaway-Sant'Anna (condensed).
%  TWFE event study deferred to the Online Appendix.
%  Companion code: event-study-CS-main.do, referee-round2.do
% ---------------------------------------------------------------

% Nested under "Data and empirical strategy".
\subsection{Empirical strategy}\label{sec:empirics_cs}

I estimate dynamic spillovers with the staggered difference-in-differences estimator of \citet{Callaway2021} (CS). Because the focal threshold crossings occur at staggered dates, a two-way fixed-effects (TWFE) event study would recover a weighted average of cohort-by-period effects whose weights can turn negative under treatment-effect heterogeneity \citep{deChaisemartin2020,Goodman-Bacon2021}; the CS estimator avoids this. For comparability with prior FPM work I also report the canonical TWFE event study (Eq.~\ref{equation:eventstudy}) in the \hyperref[appendix:twfe]{Online Appendix}; discrepancies between the two are informative about the size of the weighting problem in my setting.\par

\paragraph{Why an event study rather than a (dynamic) regression discontinuity.}
The established design in this institutional setting is the regression discontinuity of \citet{corbi2019regional}, which compares municipalities just below and just above an FPM threshold in the year treatment status is determined; dynamic extensions that accommodate repeated crossings exist \citep{cellini2010value,hsu2024dynamic,ruggieri2025dynamic} and rest on the comparatively weak continuity assumption. I deliberately depart from that template because my estimand is different in two respects. First, the treated unit is not the municipality whose population crosses the cutoff but its \emph{neighbour}: the running variable (the focal's population distance to its threshold) is a covariate of the focal, and localising the comparison in that variable would identify the spillover only for neighbours of marginal crossers while discarding the event-time variation --- the staggered timing of crossings across cohorts --- that identifies the \emph{dynamics} of the neighbour's response, which is the object of interest here. Second, my treatment is a \emph{sustained} crossing (the $3{+}3$ bracket-stability rule of Section~\ref{sec:data}), a feature of the focal's population path over seven years rather than of its position relative to the cutoff in a single year. The price of this design is well understood: I trade the continuity assumption for a parallel-trends assumption between treated and not-yet-treated neighbours, pool crossings at different thresholds (and hence municipalities of different sizes) into one binary event, and use observations that are not local to any cutoff. I therefore devote Section~\ref{sec:identification} and the robustness battery of Section~\ref{sec:robustness} to the parallel-trends side of that trade, report cohort-and-threshold composition transparently (Table~\ref{table:referee_flow}), and flag a dynamic regression discontinuity in the spirit of \citet{cellini2010value} --- which would also accommodate the repeated crossings my sample rules exclude --- as the natural complementary design for the focal's \emph{own} dynamic response, where the running variable and the treated unit coincide.\par

Let $i$ index a neighbour municipality (after the one-pair-per-neighbour collapse of Section~\ref{sec:data}), $t$ calendar years, and $G_i$ the year in which $i$'s identifying focal partner first crosses an FPM coefficient threshold upward and stays in the new bracket for three years; the $3{+}3$ stability rule and the $1999$--$2014$ panel bound the cohorts to $G_i\in\{2002,\dots,2011\}$, and neighbours whose focals never qualify are never treated, denoted $G_i=\infty$ following the notation of \citet{Callaway2021}.\footnote{In the companion code the never-treated group is stored as $G_i=0$, the convention of the \texttt{csdid} software; throughout the text I use the standard $G_i=\infty$ notation for the same set of neighbours.} For each (log) outcome $Y_{it}$ I estimate the group-time average treatment effects on the treated,
\[
\mathrm{ATT}(g,t)=\mathbb{E}\bigl[\,Y_{it}(1)-Y_{it}(0)\bigm|G_i=g\,\bigr],\qquad t\ge g,
\]
by the doubly-robust estimator of \citet{SantAnnaZhao2020}, with the \emph{not-yet-treated} comparison group --- never-treated neighbours ($G_i=\infty$) together with neighbours whose identifying focal partner has not yet crossed as of year $t$ ($G_i>t$). Here $G_i$ refers to the focal partner's crossing, not to any change in the neighbour's own FPM bracket. Identification rests on parallel trends between treated and not-yet-treated neighbours; standard errors come from the influence function and are clustered at the neighbour level (Section~\ref{sec:robustness} confirms robustness to microregion-level clustering, which addresses the spatial correlation induced by a focal shock reaching several neighbours, and Table~\ref{table:referee_boot} to replacing the analytic standard errors with a multiplier bootstrap).\par

\paragraph{Aggregation: the estimands I report.}
I report two aggregations of the $\mathrm{ATT}(g,t)$, both from \citet[Sec.~3.1]{Callaway2021}. The event-study path plots
\[
\theta_e \;=\; \sum_{g:\; g+e\,\in\,[1999,\,2014]} \mathbb{P}\bigl(G_i=g \bigm| G_i+e \in [1999,\,2014]\bigr)\; \mathrm{ATT}(g,\,g+e),
\]
the average effect $e$ years after (or, for $e<0$, before) the focal's crossing, averaging over the cohorts observed at event time $e$ with weights proportional to cohort size; I report $\theta_e$ for $e\in\{-4,\dots,3\}$ in percent units (log coefficients $\times100$) with 90\% confidence intervals. The single-number \emph{overall} ATT that I quote in the text and tables is the \emph{simple} weighted average of all post-treatment group-time effects,
\[
\theta^{\mathrm{simple}} \;=\; \frac{\sum_{g}\sum_{t \ge g} \mathbb{P}(G_i=g)\,\mathrm{ATT}(g,t)}{\sum_{g}\sum_{t \ge g} \mathbb{P}(G_i=g)},
\]
i.e.\ each cohort-by-year cell $(g,t)$ with $t\ge g$ enters with weight proportional to the cohort's share of the treated population, so cohorts treated earlier (observed for more post-event years) contribute more cells. It answers: \emph{by how much, on average over the observed post-event window, does a treated neighbour's outcome exceed its no-crossing counterfactual?} Every table reporting an overall ATT restates this definition in its notes.\par

\paragraph{Pre-event coefficients: what the leads do and do not test.}
The leads $e<0$ in my event-study figures are estimated with the \texttt{csdid} default --- a \emph{varying} base period and short differences --- so each lead is a pseudo-ATT comparing adjacent pre-event years; as \citet{Callaway2021} note, these are informative about the plausibility of \emph{no anticipation} rather than a direct test of parallel trends, and the typically omitted $e=-1$ coefficient is reported rather than normalised to zero. To assess pre-trends directly I re-estimate every headline outcome with a \emph{universal} base period and \emph{long} differences --- each coefficient, pre- and post-event, measured relative to the period before treatment ($g-1$) --- which restores the specification most familiar from the linear event-study literature; Table~\ref{table:referee_long2} reports these long-difference leads together with two joint Wald tests --- one on the aggregated event-time leads the figures display, one on all disaggregated pre-treatment $\mathrm{ATT}(g,t)$ cells --- and Figure~\ref{figure:long2} plots the corresponding event-study paths for the four outcomes that carry the paper's conclusions; Section~\ref{sec:identification} discusses what these diagnostics do and do not support. The outcome set is fixed in advance and spans demographics (neighbour population, which doubles as the reverse-causation test), the fiscal block (the complete expenditure and revenue decomposition of Table~\ref{table:referee_budget}, with current and education expenditure and federal transfers ex-FPM as the headline series), the labour market (public- and private-sector employment) and firm dynamics (the total firm count and its services-sector decomposition). The estimation sample, treatment definition and clean-comparison restriction are exactly those of Section~\ref{sec:data}; realised sample sizes appear alongside each estimate in Section~\ref{sec:results}.\par