Researchers who study online polarization often run a simple test on who-retweets-whom graphs. Drop a random walker on one side of the graph and ask how often it ends up at the other side's most influential accounts. When it almost never crosses, the debate is called controversial. Studies that repeat this test over months report that debates "harden" during crises and attention spikes. Every one of these scores, however, is computed on whoever happens to be posting in a given time window. If moderate users who connect the two sides get exhausted and stop posting, the bridges disappear from the graph. The walker then becomes trapped even though nobody changed their mind. Clinical researchers know this pattern well as survivor bias. In glioma cohorts, average cognition looks stable because the patients who decline drop out (Maureen Parkinson et al.). Network controversy research has no equivalent correction.
We propose to split any change in a random-walk controversy score between two time windows into three parts. The first is rewiring among users present in both windows: genuine change in who endorses whom. The second is the removal of users who left. The third is the addition of newcomers. We then estimate what the score would have been had the leavers stayed, by reweighting the users who remain according to how likely each was to leave given their position in the graph. The deliverable is a measurement tool and a re-analysis of published longitudinal findings. Its central output is a number for how much of reported hardening is composition rather than conversion.
Core Claim
The Random Walk Controversy score (RWC), introduced in Quantifying Controversy on Social Media, is computed as follows. Split the endorsement graph into sides $A$ and $B$, and let $P_{XY}$ be the probability that a walker starting on side $X$ ends at a high-degree hub of side $Y$. The score is
$$\mathrm{RWC} = P_{AA}P_{BB} - P_{AB}P_{BA}.$$
The original paper shows the score is insensitive to overall user volume. Volume is not composition, though, and nothing in RWC protects it from which users are present. Our claim is that RWC changes over time can be attributed exactly to three factors: continuer rewiring $R$, exits $E$, and entries $N$. The attribution averages each factor's marginal effect over the orderings in which the factors are switched on, which is a Shapley split over three players:
$$\Delta \mathrm{RWC} = \phi_R + \phi_E + \phi_N.$$
Each $\phi$ is computed by evaluating RWC on counterfactual graphs. One example is the time-$t$ graph with the leavers deleted but continuers' edges left unchanged.
We also claim that, in real debates, exits are not random with respect to graph position. Boundary users exit at higher rates than hub users. Boundary users are those with at least one cross-side edge, following A Measure of Polarization on Social Media Networks Based on Community Boundaries. Hub users are those deep inside a camp. If this holds, $\phi_E$ is positive, and naive snapshot RWC overstates how much individuals radicalized.
We make two concrete, falsifiable predictions from published observations. The first concerns the Italian vaccine debate in Echoes through Time. That paper reports RWC between 0.95 and 0.99, a vanishing neutral cluster, and only 1.9% of hesitant users moving to the supportive camp. We predict that the neutral cluster disappeared mainly through exit, not migration. The second concerns attention spikes in The Ebb and Flow of Controversial Debates on Social Media. We predict that the higher RWC in high-volume windows comes largely from entry: a flood of one-off users who retweet only their own side's hubs. Collective attention would then change who is in the graph more than how people behave.
A null result is equally informative. If $\phi_E$ and $\phi_N$ are near zero, the hardening literature is vindicated on firmer ground.
Research Program
Defining exit in a noisy setting. The first component handles the fact that "leaving" is not directly observed. Absence from a topic graph can mean three things: the user left the platform, left the topic, or was simply not captured by a 1% sample, as in the 57-month corpus. We define exit as no on-topic activity for $k$ consecutive windows. We then calibrate baseline churn using the non-controversial control hashtags (#ff, #tbt, #sxsw, #nfl) from the same corpus. Those topics show flat RWC, so their exit rate gives a reference for sampling-induced and generic churn. Exit "excess" in controversial topics is measured against them. Where off-topic activity is visible, we separate topic exit from platform exit. That distinction matters substantively: a moderate who still posts about football but stopped posting about vaccines is a different phenomenon from an account that went silent.
Modeling who leaves. The second component models exit as a function of graph position. The predictors are boundary status and the internal-to-external edge ratio from Guerra et al. They also include the hitting-time polarity score $\rho(u) \in (-1,1)$ from Mary, Mary, Quite Contrary, degree, and prior activity. This is the step the attrition literature never takes. Methods such as the quadruply robust estimator in Policy Learning for Balancing Short-Term and Long-Term Rewards and the proximal bridge estimator in Proximal Survival Analysis for Dependent Left Truncation treat units as independent rows. Here, by contrast, a unit's exit probability depends on, and changes, the walk statistics of everyone else.
Correcting the score. The third component is the counterfactual "retained-population" RWC. Each continuer's outgoing transition mass and hub eligibility are reweighted by the inverse of their estimated staying probability. The walk then represents the population that would have been present without selective exit. The correction rests on an assumption we state openly: exit depends only on observed graph position and history. That assumption is untestable, as both Wu et al. and Wang, Ying and Xu emphasize. We therefore report sensitivity bounds rather than a single corrected number. We borrow the proxy logic of the proximal estimator: off-topic activity serves as a proxy for unobserved fatigue, which plausibly drives both topic exit and later behavior. We do not attempt full proximal identification on graphs. That is a stated stretch goal, not a promise.
Partition drift. The last component deals with the fact that RWC depends on the partition, a limitation acknowledged in the original paper. Re-running community detection in every window would mix partition noise into $\phi_R$. Continuers therefore keep their side label unless their polarity score crosses zero. Newcomers are assigned by majority endorsement. Fully re-partitioned results are reported as a robustness check.
Baselines
The naive reference point is per-window snapshot RWC on whoever is present, exactly as in Echoes through Time. The reported figure to compare against is RWC "consistently between 0.95 and 0.99" across six periods on the Italian vaccine data. We recompute it with the same Paris partitions to confirm we reproduce that range before decomposing it. "Beating" this baseline does not mean producing a higher or lower number. It means showing on synthetic data with planted ground truth that snapshot RWC attributes exit-driven change to radicalization, while our decomposition does not.
The strongest existing method for asking "did individuals change?" is the balanced-panel score: RWC computed only on users active in every window. Researchers use this routinely as a fix. It runs on identical graphs and partitions at negligible cost. To beat it, our retained-population score must recover planted population-level RWC with lower error when exit is position-dependent. We expect the balanced panel to be accurate for the stayers but biased for the population. No reported result was found on Lacuna for a balanced-panel or attrition-corrected RWC on any of these corpora, so that comparison is new.
A third baseline carries departed users' last observed edges forward into later windows. This is last-observation-carried-forward, the network analogue of the simple imputation that Optimal intensive care outcome prediction over time using machine learning found inadequate under dynamic selection.
We also compare against boundary polarization $P$ from Guerra et al. computed per window. This tests whether a boundary-based metric is less sensitive to composition than RWC. Guerra et al. report, for example, $P=-0.14$ between Liberals and Independents in gun control.
The key ablation removes graph-position features from the exit model, keeping only activity and tenure. This isolates the claim that network position is what makes the correction work.
Why not just…?
Why not just compute RWC on the balanced panel and stop? This is the most serious alternative. The rewiring component $\phi_R$ is essentially that computation. But the balanced panel answers a narrower question: how much did the survivors change. Survivors are selected, and a graph of only continuers contains walks that never existed in the real population. In the Crosscheck sensing study, a continuous-compliance filter cut 61 participants to 13 (Assessing the relationship between routine and schizophrenia symptoms). On 57-month data a balanced panel may be similarly tiny and peculiar. The synthetic experiments settle this directly. If the balanced panel matches the reweighted score in recovering population RWC under realistic exit patterns, we will report the cheap method as sufficient and keep only the decomposition.
Why not just track modularity, which is cheap and less fragile? Guerra et al. show that modularity cannot separate antagonistic from benign clustering: Brazilian soccer and NYC sports had similar modularity but opposite boundary polarization. Moreover, modularity is just as composition-dependent as RWC. Switching metrics leaves the survivor problem untouched. The decomposition applies to any metric, and we run it on $P$ as well.
Why not just impute leavers' edges or assume dropout is random given activity? Random-given-activity exit is exactly the ablation without position features. If it matches the full model, our central mechanism claim fails. Carried-forward edges assume leavers would keep their old endorsements. That assumption is implausible for users who left because of the conflict, and it will be tested on the planted-ground-truth data.
Proposed Experiments
Synthetic tests with known answers. We start from real retweet graphs from the 2015 ten-topic Twitter collection (roughly 1,600 to 9,400 nodes per graph, per Reducing Controversy by Connecting Opposing Views). We then simulate multiple windows under three regimes. In the first, opinions are fixed and boundary users have elevated exit hazards. In the second, attrition is uniform and genuine rewiring occurs. In the third, high-volume windows are flooded by single-side newcomers. Metrics are attribution error for $\phi_R$, $\phi_E$ and $\phi_N$ against the planted truth, and the absolute error of each estimator in recovering population RWC. Under the first regime, the decisive check is that snapshot RWC rises while our $\phi_R$ stays near zero.
Re-analysis of the Italian vaccine debate. On the Italian COVID-19 data, the decisive checks are two. First, whether the exit hazard is significantly higher for neutral and boundary users than for hub users after subtracting control-topic churn. Second, what share of the neutral cluster's disappearance $\phi_E$ accounts for. We will also test whether retained-population RWC falls measurably below the 0.95–0.99 range.
Re-analysis of the 57-month corpus. On the 57-month corpus we repeat Garimella et al.'s ten volume buckets. We test whether the rise of RWC with volume is mostly $\phi_N$. Control topics must show near-zero excess exit and flat components; failure there would indicate that our exit definition is capturing sampling noise.
Robustness. We report the size of the unobserved-fatigue effect that would erase any $\phi_E$ we find, using off-topic activity as the proxy. We also report results under re-partitioning instead of fixed labels.
What changes the agenda. A positive finding would mean that work on bridging interventions such as RePBubLik (RePBubLik), ROV-AP, and contrarian recommendation is evaluated against a moving, self-selecting population. Retention of boundary users would then become an objective in its own right.
References
- A longitudinal prospective study investigating cognitive function in patients with high grade glioma
- Quantifying Controversy on Social Media
- A Measure of Polarization on Social Media Networks Based on Community Boundaries
- Echoes through Time: Evolution of the Italian COVID-19 Vaccination Debate
- The Ebb and Flow of Controversial Debates on Social Media
- Mary, Mary, Quite Contrary: Exposing Twitter Users to Contrarian News
- Policy Learning for Balancing Short-Term and Long-Term Rewards
- Proximal Survival Analysis for Dependent Left Truncation
- Optimal intensive care outcome prediction over time using machine learning
- Assessing the relationship between routine and schizophrenia symptoms with passively sensed measures of behavioral stability
- Reducing Controversy by Connecting Opposing Views
- RePBubLik: Reducing Polarized Bubble Radius with Link Insertions