\section{Empirical design}
\label{sec:design}

\subsection{The estimand}

For an outcome $Y$ from Section~\ref{sec:outcomes}, define the within-event
change $\Delta Y_{i,t}(h) = Y_{i,t}(h) - Y_{i,t}(-5)$, where $Y_{i,t}(-5)$
denotes the same outcome evaluated five minutes before the event. The
baseline estimand is the difference-in-differences
\begin{equation}
\Delta\Delta Y(h) \;=\;
\mathbb{E}\big[\Delta Y(h)\,\big|\,\text{real event}\big]
\;-\;
\mathbb{E}\big[\Delta Y(h)\,\big|\,\text{matched placebo}\big],
\label{eq:dd}
\end{equation}
estimated as the difference between the two arms' sample means. In
potential-outcomes language, the placebo arm estimates the path of
cross-sectional activity that the event window would have followed had the
source stock not moved, holding fixed the stock, the minute of day, the
month, and the calm-market state. Three biases that a naive event study would
absorb are differenced out explicitly. \emph{Volatility clustering}: shocks
arrive in already-active minutes, so post-event activity is elevated even
absent transmission; the inner difference removes the level.
\emph{Deterministic intraday drift}: breadth trends over the trading day; the
placebo, matched on minute of day, follows the same drift.
\emph{Filter-induced selection}: conditioning on a calm market at $t$ selects
minutes followed by reversion toward normal activity; the placebo is drawn
under the identical filters and inherits the identical reversion.

The inner difference has a cost that we quantify rather than assume away. If
real events select minutes whose ambient activity is elevated for transient
reasons, part of that elevation reverts over the following minutes, and
$\Delta\Delta$ is biased downward by the reversion. We therefore report,
alongside~\eqref{eq:dd}, the post-event level difference without
pre-differencing and a stratified estimator that compares real and placebo
post-event levels within deciles of the pre-event level,
\begin{equation}
\widehat{\theta}^{\,S}(h) \;=\; \sum_{b=1}^{10} w_b\,
\Big(\bar Y^{\,\mathrm{real}}_{b}(h) - \bar Y^{\,\mathrm{placebo}}_{b}(h)\Big),
\qquad w_b = \frac{n^{\mathrm{real}}_b}{\sum_{b'} n^{\mathrm{real}}_{b'}},
\label{eq:strat}
\end{equation}
where $b$ indexes deciles of $Y_{i,t}(-5)$ over the pooled sample. Because the
placebo arm has a lower latent activity level than the real arm within any
stratum defined on a noisy pre-event measurement, regression to the mean
pushes~\eqref{eq:strat} upward; the two estimators therefore bracket the
market-wide response from below and from above.

\subsection{Placebo construction}

For each real event $(i,t)$ the matched placebo is drawn as follows, with a
fixed seed recorded in the replication package. The candidate set collects all
minutes of the same month with the same minute of day $\tau(t)$ on a different
trading day at which security $i$ has an observable return with
$|z_{i,\cdot}|<2$, the market-calm filter holds, and the simultaneity filter
holds. One candidate is drawn uniformly at random, and every outcome of
Section~\ref{sec:outcomes} is computed at the placebo minute by the identical
code path. The placebo is labelled with the real event's magnitude and sign so
that all conditional cuts---by $|z|$ bin, by sign, by number of co-arriving
events---compare real and placebo events within the same cell. Events with an
empty candidate set contribute to the real arm only; the match rate is
\MatchRate\% over the full sample, \MatchRateNineties\% in the 1990s, when
calm candidate minutes with an observable return are scarcer, and at least
\MatchRateMinPost\% in each later decade. The placebo is not
matched on the pre-event level of the outcome, which is why the pre-event
levels of the two arms can differ and are reported.

\subsection{Inference}

Outcomes are correlated across events within a trading day---mechanically so,
because events of the same minute share receivers and \MeanCoArrival{} source
events on average share each event minute---and within a source security
across days. All inference therefore resamples clusters: for
$b=1,\dots,500$, draw event dates with replacement, recompute date-level sums
and counts for both arms, and form the bootstrap distribution of the full
statistic. Standard errors are bootstrap standard deviations. Two
alternatives are reported: a month-cluster variant (resampling year-months),
which roughly doubles the standard error of the network differential without
changing any conclusion, and a ticker-cluster variant (resampling source
securities), which more than doubles it. With \EventDays{} event days and
\NEventsRealMM{} million events, the minimum detectable effect for
market-wide breadth at $h=5$ at the 5\% level with 80\% power is about
\MDEFive$\times10^{-4}$, or one additional responding security per
\MDEEventsPer{} events given \NEligMean{} observable receivers on average.
Null results below are powered nulls in this sense.

\subsection{Identification: what is and is not claimed}

The design identifies the predictive association between an isolated
idiosyncratic extreme and subsequent cross-sectional tail activity, purged of
intraday seasonality, calm-market selection, and the stock's own base rates,
and bounded with respect to ambient-activity selection as described above. It
does not identify the structural channel behind the network differential:
lagged-correlation neighbors are typically industry peers, ETF co-members, and
factor-exposure twins, and the differential aggregates fundamental
information transmission (investors repricing linked firms on the same news)
with trading-channel transmission (basket flows, hedging, liquidity
withdrawal). Separating those requires timestamped news and order-flow data
and is beyond OHLCV bars; the paper's claims are phrased as predictive
propagation, not causal transmission. Likewise, the systemic co-jump series
conflates common news arrivals with endogenous synchronization; we document
its evolution and severity without attributing minutes to either source.

\subsection{Falsification and diagnostic battery}

Five checks are reported. (1) \emph{Pre-event levels}: the levels of every
outcome at $t-5$ in the two arms, with their difference; a non-zero
difference is not a failure of the design but a measured quantity that the
estimators above handle in different ways. (2) \emph{Placebo network
contrast}: the neighbor-minus-other contrast computed on placebo events
alone, over the full sample and by decade. (3) \emph{Announcement windows}:
excluding the 10:00 and 14:00--14:30 ET windows that host most scheduled
releases. (4) \emph{Coverage}: fixed-rule lagged universes make the 2020
source-coverage expansion irrelevant to any comparison. (5)
\emph{Tick regime}: the post-decimalization subsample is reported for every
headline estimate. Tables~\ref{tab:design_checks},
\ref{tab:network_components}, and~\ref{tab:robustness} quantify each.