Table A.7 tests this. I measure turnover as a cross-bloc handover between appointment and delivery. The report is appointed under one bloc and delivered under the other. This is fixed before any implementation, so it does not depend on how long a provision takes to enact. I then regress full enactment on a distributive indicator and its interaction with the cross-bloc handover, with commission fixed effects. The coefficient on the interaction between the distributive indicator and the cross-bloc handover measures how much more distributive provisions are trimmed when there was a handover, compared to when there was not. The cross-bloc indicator is the same for every provision in a report. Its own effect is therefore absorbed by the fixed effects, and only the interaction is identified. The interaction is not statistically significant. The trim is no larger for reports that change hands between blocs during the commission's work. The point estimate leans slightly more negative under a handover, but I cannot reject equality, and the test is underpowered. The trim thus looks like a structural regularity rather than an artifact of which bloc inherits the report.

Distributive provisions might be scaled back only when the government changes during the commission's work.

One worry is that this trimming reflects political turnover rather than the nature of the provisions themselves.

Typical examples are “Departementet kan gi nærmere bestemmelser om valglistenes innhold” (NOU 2001:3, the ministry may set detailed rules on the content of electoral lists), “Departementet kan i forskrift fastsette nærmere regler om oppbevaringen” (NOU 2017:15, the ministry may set detailed rules on retention by regulation), and “Kongen kan gi nærare forskrifter til gjennomføring av lova” (NOU 2018:11, the King in Council may issue regulations to implement the act). Each leaves the substance of the rule to be fixed later by the executive. ↩

I exclude three cases that do not grant genuinely new rule-making power: a reference to regulations that already exist (“forskrifter gitt i medhold av denne lov”), a permissive “kan” describing something that may happen, and a rule-making right granted to a private party.

Without the truncation correction the figure is a still-substantial κ=0.70 (90%).

Two earlier, fuzzier proxy dimensions (a technical-versus-ideological code and a fiscal-cost code) were piloted but are not used in the paper.

The matching does record reworded text as fully implemented, so this reflects the number of distinct requirements a provision packs in, not rewording as such.

Studying it adds depth to the earlier results rather than qualifying them.

The larger raw gap in the pooled data, where delegating provisions are adopted about eight points more often (Appendix Table A.6), is a between-report artifact: reports that contain more delegating provisions have higher adoption for other reasons, but within a report a government treats a provision no differently for handing it discretion.

Delegating provisions are shelved marginally less often than others in the same report, but the gap is small and insignificant (−1.6 percentage points, p=0.22) and does not survive controls (−1.0, p=0.44); the trim margin is essentially zero (−0.2 percentage points, p=0.90)

Panel B takes the opposite kind of content, provisions that delegate rule-making power (Cohen's κ=0.70 against blind hand labels).

The longer a provision's text, the more of it there is to reword when it is enacted, so a longer provision is more likely to be scored as a partial rather than a full match even when its substance is adopted

This is the same back-end selection studied above, measured at a finer margin, and a more credible one

I measure both dimensions with the same labelling pipeline and validation as the rest of the paper (Appendix B), applied to each of the 9,453 §-level provisions.

I classify each of the 9,453 §-level provisions as efficiency-oriented, distributive, or mixed, using the same labelling pipeline and validation as the other provision dimensions (Appendix B)

Provisions coded distributive include the inheritance- and gift-tax schedules in NOU 2000:8, which fix the rates paid by different classes of heir, and the introduction-benefit rules for newly arrived immigrants in NOU 2001:20, which set who qualifies for a state transfer and how large it is—each determines who gains and who loses. Efficiency-oriented provisions, by contrast, are ones on which the affected parties share the objective and differ only over means: procedural and administrative rules such as how a court records and announces a decision, deadlines and notification requirements in case processing, or the harmonisation of a legal definition across statutes. The distributive provisions move resources or rights between identifiable groups; the efficiency provisions do not.

For a standing commission that produces many reports, such as Banklovkommisjonen, this is the government in office when the ministry assigned that report, not the commission's founding date.

Throughout this section I exclude standing commissions—permanent expert bodies such as Banklovkommisjonen that report across many governments, and so have no single appointing government against which a handover can be defined—together with a few reports whose appointing or delivering government is indeterminate, leaving 129 reports.

n together, the evidence is consistent with insulation: adoption does not move when political control changes hands, whether a report is inherited by the opposing bloc or, within a stable government, by a different minister. The estimates are underpowered—with 129 commissions, 42 cross-bloc cases, and far fewer in the minister categories, I cannot rule out modest disruption—so I read this as the absence of the large effect the selection account predicts rather than a proven null. It is also the strongest evidence against a purely selection-driven reading of the high adoption rate: reports inherited by political opponents are adopted at the same rate as those delivered to their sponsors.

. I also test a finer margin—whether, within a stable government, the responsible minister changed, in the governing party or across coalition parties—and it too is never significant; but with as few as 10 cross-party reports these same-government cells are too small to support inference, so I report that analysis in Appendix Table A.6 rather than featuring it here.

This is the sharpest test of insulation: if adoption reflected the appointing government's own preferences—the selection account—a report should be most vulnerable precisely when opponents take over before it is delivered

The one feature that predicts adoption—being asked to draft law—is thus insensitive to how the regression is specified, and the uniformity of everything else does not hinge on a particular control set.

The figure fixes one set of controls, so a single significant coefficient could in principle be an artifact of that choice.

most such questions were put before any provision had even been enacted (16 of the 31 I can date).

and in several cases adoption followed the pressure,

And the challenge row stays empty across both under-adopted columns:

Reading Table 5 column by column shows the pattern. Within each adoption band, demands to act are the dominant stance for reports adopted below 75%—they are the most common response to both low- and partially-adopted reports—whereas questions about fully-adopted reports are mostly passing citations.

These are obstacles to turning a report into law, not objections to its content.

Second, across all the questions now—not just the few a minister answered with a reason—the stance is to push the reform forward, not to oppose it.

One limitation is that the sample contains only the questions that name a report, so it captures follow-up rather than all the attention a report draws; what counts, then, is the near-absence of challenges, not the raw number of demands.

The questions let me see which. They are an imperfect window—I return to their limits below—but they are the one source that speaks to the shelved reports directly.

I expect them to be informative precisely because a shelved report is not a closed matter: were it quietly rejected on the merits, one would expect criticism; were it merely stuck, one would expect prodding.

The commission was itself divided on whether the proposed defined-benefit pension product was desirable; sent to høring (2015), not taken forward. (Earlier “industry called it unnecessary” claim is in the høring responses — not yet confirmed.)

The committee recommended that Norway ratify the Rotterdam Rules convention; the convention has not entered into force and Norway has not ratified, so there is nothing to enact.

Commission delivered with marked dissent on the core compensation question; the minister said a bill was expected but it was “too early to say when.” No bill has followed.

Full standardisation was not adopted; only a narrow part (standardised income-loss compensation for children) was enacted later (2015).

Minister: report delivered with marked dissent on the core question; a bill is expected but cannot be timed. (Your 'høringssvar' hypothesis is NOT confirmed by this answer — would need the consultation record.)

Resulting §5 structure (each section = an answer to "when does the government reclaim authority?")

Name the HARKing honestly. The distributive cut was theory-motivated after the fiscal-cost hint; the framework organizes patterns, several found inductively. Don't sell post-hoc organization as ex-ante prediction. The pre-specified battery + blind κ are what make it credible anyway.

Tier 2 — descriptive facts the framework is silent on Reported as facts, explicitly flagged as not derived from the framework; some as open puzzles / future work. The polarized distribution shape; the magnitude of the mandate-type gap (+12.4pp); the time-to-adoption profile; the non-monotonicity of parliamentary attention (dead NOUs draw less than partials); the Lovdata counterfactual share. Don't force these through one model; don't suppress them because no model predicts them.

Maskin–Tirole (2004)

lobbying section

4 — organized losers +3.1pp adopted (p=.011); distribution→FULL sharpens to −7.0pp once losers controlled (separable)

Majone (1999)

n the language of Aghion–Tirole, the government always holds formal authority (only it legislates); the commission, through information and drafting, can hold real authority over content.

how is law-making authority distributed between elected governments and the expert bodies they commission — and when does the government reclaim it?

The modest gradient we observe is consistent with the filing event itself being a sufficiently public signal in both environments, perhaps amplified locally by social networks and party channels that do not require formal media intermediation.

, plausibly reflecting the COVID-delayed election and shorter follow-up window.

A Supplementary analyses

Three patterns stand out. The office breakdown is sharply asymmetric: councillors lose mostly on the extensive margin (a −4.5pp registration penalty against a −1.6pp penalty for mayors), while mayors lose mostly on the intensive margin (a −3.3pp vote-share penalty against an essentially null councillor vote-share coefficient). The election coefficient is similar across offices (−2.9pp mayors, −3.8pp councillors). The reference-election panel is roughly flat at −3.3pp / −3.5pp / −3.3pp on Running for 2008/2012/2016 and drops to −1.2pp (not statistically significant) for 2020. The 2020 attenuation may reflect the COVID-delayed election and shorter follow-up window. The plaintiff panel produces an unusual ordering: prosecutor-only and third-party filings carry similar registration penalties (−3.1pp each), municipality-only filings slightly smaller (−2.5pp), and joint prosecutor-plus-municipality filings are near zero (−1.1pp, not statistically significant). The reading is murky. Prosecutor-only as the strongest is consistent with the voter-information channel (credibility scales with prosecutor independence), but the muted prosecutor-plus-municipality coefficient and the close pros-only / muni-only gap leave a political-targeting contribution open.

, taken from the project’s media database

Appendix C reports a donut regression discontinuity at the candidate registration cutoff that returns a null result with wide confidence intervals. We read this as evidence that the filing channel does not operate sharply at the registration deadline itself, leaving slower-acting candidate-side or party-side adjustments over the longer pre-election horizon as the more plausible carrier of the filing association.

The prosecutor-only ≥ municipality-only ordering is the qualitative signature the voter-information channel predicts: the credibility of the misconduct signal scales with the independence of its source, so a filing by an independent prosecutor moves the political environment more than the equivalent filing by the municipality. That municipality-only filings nonetheless carry a meaningful penalty (rather than the null one would expect under a fully political-targeting reading) bounds, but does not rule out, a political-endogeneity contribution.

A decomposition of the Panel A coefficient by plaintiff identity (Panel F of Appendix Table A.5) sharpens this reading.

The filing margin carries the largest and most robust descriptive association on registration and election (3.3 pp and 3.4 pp in the demanding court-environment specification); conditional on filing, the acquittal arm shrinks close to zero within court-environment fixed effects while the conviction arm retains a meaningful negative point estimate close to the filing estimate, but the Wald test for equality remains non-rejecting in the smaller case-level sample; the IV on the conviction margin is small and statistically null but not precise enough to rule out moderate effects.

Abstract

E Post-LASSO IV: sparsity diagnostics and alternative estimators

The filing event co-occurs with media and civil-society attention that itself moves voters, so the Panel A coefficients bundle the formal-filing footprint with that attention footprint.

The publicity caveat discussed at length in Section 4.3 also applies here.

; the nine politician-history controls are added in the appendix robustness specification (Table D.1). LASSO uses the BCCH penalty (Belloni et al., 2012); inference follows Chernozhukov et al. (2018).

Predetermined politician-history controls enter Appendix Table D.1 as a precision-adjustment robustness, but do not enter the headline.

; the side-by-side comparison with the LASSO instrument is in Appendix Figure D.1.

Appendix Table D.1 confirms that absorbing all nine controls in the second stage leaves the headline IV unchanged.

e; alternative first-stage estimators (LASSO, Ridge, no-selection benchmark) are reported in Appendix E.

Cross-estimator balance and selected-feature diagnostics for the alternative first-stage estimators are in Appendix E.

Section 4.2 shows that pre-election conviction adds little detectable association with electoral outcomes once court-environment fixed effects are absorbed. This null has two readings. It could reflect a true absence of any causal effect, or a true negative effect offset by selection on case-progression speed (which depends on judge workload, efficiency, court congestion, and case complexity, all of which may correlate with electoral prospects). To distinguish these, we use an instrumental-variables strategy that exploits the random assignment of improbidade cases to court units within each judicial district.

The per-office breakdown in Appendix Tables A.2 and A.3 shows distinct margins across offices. In the mayor subsample, the column (3) coefficients are roughly −1.6pp on registration, −2.9pp on being elected, and −3.3pp on vote share. In the councillor subsample, the registration coefficient is much larger (−4.5pp) and the election coefficient about as large as for mayors (−3.8pp), while the vote-share coefficient is essentially zero (−0.3pp). Mayors lose mostly on the intensive margin (vote share); councillors lose mostly on the extensive margin (whether to run again). The vote-share pattern reflects the structurally different denominators of the two races. Mayoral races allocate one seat per municipality, councillor races allocate many, so the average councillor vote share is mechanically much smaller. The Panel B conviction–acquittal gap differs across offices. In the mayor subsample, the Wald test rejects equality of conviction and acquittal coefficients on all three outcomes in columns (1)–(2) but on no outcome in column (3); the acquittal coefficient on Elected is positive at roughly three percentage points in columns (1)–(2). In the councillor subsample, the Wald test rejects equality only on Running in columns (1)–(2) and on no outcome under the demanding court-environment specification.

Panel B (Pre-election disposition). Under base fixed effects (column 1), conviction and acquittal coefficients are both significant and the Wald test for βconv=βacq rejects equality on all three outcomes. Conditioning on court-environment fixed effects in column (3) shrinks both coefficients toward zero and the Wald test fails to reject on any outcome. The spec-(3) failure to reject is coefficient movement, not precision loss. The absolute gap |βconv−βacq| falls by a factor of three to six while the standard error on the gap rises by between forty and seventy percent. Both disposition coefficients move toward each other once court-environment variation is absorbed, consistent with selection on a court-level dimension (likely case-resolution speed) being soaked up by the court-environment fixed effects. The result is robust to within-politician multiplicity weighting. Appendix Table A.4 collapses to one observation per politician per next election, retaining each politician’s earliest pre-election disposition, and the qualitative pattern is unchanged.

The raw correlations in column (1) are informative for a different reason. Filed politicians are essentially as likely as the unfiled to register at the next election (the registration coefficient is small and statistically insignificant) but already 1.4pp less likely to win and 2.0pp lower on the unconditional vote share. Conditioning on the politician’s career trajectory at the reference election (column 2) makes the negative association on registration emerge and grows the election coefficient further. The reversal is what one would expect under positive selection on the treatment. Politicians who attract improbidade filings are disproportionately career-active. They hold visible incumbent positions, so the unconditional registration rate of filed politicians is mechanically high. Once we hold career trajectory fixed, that selection is absorbed and the negative filing–registration association shows through. Adding the judicial-district-by-reference-election-year fixed effects in column (3) leaves the column (2) coefficients essentially unchanged, ruling out court-environment heterogeneity as a confounder. Adding pre-determined politician controls in column (4) (demographics, anchor-election party and education fixed effects, prior vote share and margin, coalition size, log campaign expenditure, log declared wealth, and log receipts) leaves the registration coefficient at 3.4 pp and the election coefficient at 3.6 pp. The headline filing association is therefore not absorbed by un-modelled politician selection on observable pre-treatment characteristics.

First-time / never-won candidates are excluded;

Sample definitions are in Section 3.3. Panel A of Table 3 is a politician-level panel with one observation per politician per reference election. We use four reference elections (2008/2012/2016/2020) and include every politician who is a career politician at the reference election, defined as either currently holding elected office (mayor or councillor incumbents) or having won at least one prior election, regardless of whether they ran at the reference election themselves. Including sat-out career politicians (e.g. term-limited mayors taking a forced break before running again) avoids conditioning on having chosen to run in a given cycle, which would mechanically exclude precisely the politicians the filing event may push out of the cycle. First-time / never-won candidates are excluded: an improbidade allegation against such a politician cannot be tied to a documented office tenure. The mayor subsample additionally excludes politicians who are term-limited at the next election (consecutive two-term mayoral incumbents ending at the reference cycle), since they are mechanically barred from running for mayor again at lead and their Running=0 is not behavioural. Panel B is the case-level Disposition-OLS sample: cases filed in the one-to-four year window before the politician’s next election, restricted to politicians who held office at filing time (mayor or councillor at the pre-filing election) or have any prior electoral win. The lower bound at one year excludes filings landing in the election year itself, when no pre-election disposition is feasible. The upper bound matches Panel A’s window and keeps the case-filing event term-aligned. For Panel A, filed before electioni equals one if politician i had at least one improbidade case filed against them in the one-to-four year window before the corresponding next election. For Panel B, defined at the case level, convicted before electionij and acquitted before electionij equal one if case j naming politician i was decided as a conviction (resp. acquittal) before the politician’s next election, and zero otherwise. The two indicators are mutually exclusive within a case; their common zero category is the case still being pending as of the next election (cases decided after the election cannot affect voters by definition and are equivalent to pending cases for this analysis).

For Panel A, filed before electioni equals one if politician i had at least one improbidade case filed against them in the one-to-four year window before the corresponding next election. For Panel B, defined at the case level, convicted before electionij and acquitted before electionij equal one if case j naming politician i was decided as a conviction (resp. acquittal) before the politician’s next election, and zero otherwise. The two indicators are mutually exclusive within a case; their common zero category is the case still being pending as of the next election (cases decided after the election cannot affect voters by definition and are equivalent to pending cases for this analysis).

s. Including sat-out career politicians (e.g. term-limited mayors taking a forced break before running again) avoids conditioning on having chosen to run in a given cycle, which would mechanically exclude precisely the politicians the filing event may push out of the cycle. First-time / never-won candidates are excluded: an improbidade allegation against such a politician cannot be tied to a documented office tenure. The mayor subsample additionally excludes politicians who are term-limited at the next election (consecutive two-term mayoral incumbents ending at the reference cycle), since they are mechanically barred from running for mayor again at lead and their Running=0 is not behavioural.

At each horizon h, the denominator is restricted to cohorts C with C+h≤2020, which ensures full h-year follow-up given the case data window (filing years 2012–2022) and a typical two-year decision lag. Cohorts without a full h-year follow-up window are therefore excluded from both the numerator and denominator at horizon

Improbidade exposure is therefore a mayoral-office phenomenon at the population level. For councillors, the cumulative incidence stays in low single digits across the observable horizon.

The same case-level structure, with additional randomisation prerequisites: non-missing court unit (vara) and stratum (judicial district × filing year) identifiers

The joint conviction–acquittal regression in Section 4.2 is estimated on this sample.

Per-court Diário de Justiça coverage starts around 2011 and varies by court; see Appendix Figure A.1 for the per-court coverage map and case-count density. Some downstream design choices apply tighter cohort windows because they require additional post-cohort follow-up years (e.g. the cumulative-incidence figure truncates at cohort year +8, and the registration-deadline RDD restricts to cohorts with reliable pre-deadline coverage). Those tighter windows are documented at the relevant table or figure note.

The cleaned tribunal party records also carry a CPF column populated by an earlier name-to-CPF crosswalk, but the link to the TSE panel is itself name-based.

This is the actuarial life-table estimator with administrative censoring.

— the last year the current TJSP extract covers reliably —

— mayors are exposed at roughly ten times the rate of councillors

(these reflect prior public-service roles, ongoing investigations that crystallise into filings around election time, and cases naming the politician as a candidate)

The OLS evidence in Section 4.3 uses two samples drawn from this panel.

The Filing-OLS sample (Panel A of Table 2) is a candidacy-grain sample of all incumbents at the 2008/2012/2016/2020

A pre-election acquittal is an object of separate interest — whether being cleared by the court improves a politician’s electoral prospects. The acquittal estimate is flat and, where signed, oppositely signed from the conviction estimate; the Wald test for βconv=βacq rejects equality in the base specification but not under the court-environment cell. To identify the conviction effect more cleanly, we turn to an instrumental-variables strategy

The filing association is itself only OLS-identified and cannot be cleanly separated from the publicity that typically accompanies a filing — prosecutors respond to media coverage and civil-society reports, and the same publicity may move voter and party behaviour independently — so we read it as the joint footprint of an improbidade complaint and its surrounding attention rather than as the causal effect of the filing event itself

The IV thus produces point estimates close to zero, and so does the demanding within-cell OLS specification — two approaches with very different identifying assumptions — conditional selection-on-observables for the OLS, random courtroom assignment plus exclusion for the IV — neither of which finds a detectable pre-election conviction effect

Why we exclude the 2004 and 2008 lead cohorts. Pre-2010 filings enter our case record only through their post-2010 activity — subsequent publications or decisions visible in the São Paulo electronic court diary, which launched coverage in 2009 under Law No. 11,419/2006. This coverage selection bites asymmetrically at the cutoff for early cohorts: filings arriving before the deadline ride through an active election cycle, generate sustained activity, and remain observable in the post-2010 record; filings arriving after the deadline often resolve quietly during the post-election lull and never enter the post-2010 record. Among the 2004 and 2008 lead cohorts at a 90-day bandwidth, only 38% of the post-deadline filings have a recorded decision, against 61% of the pre-deadline filings; the same imbalance is essentially zero for the 2012–2024 leads (84% versus 85%). Including the early cohorts produces a large and significant negative deadline coefficient that attenuates by 55–60% toward zero when the sample is restricted to filings with a recorded decision — the substantive signature of a selection artifact rather than a deadline effect. The 2012–2024 leads, used as the headline sample, are observed within the modern coverage window with clean balance across the cutoff.

mple, fixed effects, controls, and clustering as Table 3 Panel A. Two treatment definitions are compared. Headline (filing in [t−2,t+3]) reproduces the main-paper treatment: at least one improbidade filing in the one-to-six year window before the lead election. During-term (filing in [t+1,t+3]) restricts the filing indicator to cases filed strictly during the politician’s term, after th

Sigurd flags two concerns: (i) treated cases include defendants whose case was filed before they held the office, which is a different substantive story than “an incumbent named while in office”, and (ii) survival to the candidacy panel implicitly conditions on the politician winning the focal election, which pre-filing cases can confound.

Vara assignment + identifiable stratum.

the IV-estimation sample contains N=17,700 case–politician rows across 3,935 strata for the candidacy and election outcomes; the unconditional vote share (with non-runners coded as zero) is observable for 17,026 of these rows.

Within each bucket we extract three vara-level outcome types: the conditional conviction rate among cases that received a verdict, the conditional acquittal rate, and the average filing-to-decision time. These capture the three independently informative dimensions of vara behaviour: how often the vara convicts on the merits, how often it acquits on the merits, and how fast it disposes of cases (independent of verdict). Together this yields the 25 candidate instruments described in the next paragraph (15 rate-and-time aggregates plus 10 missing-indicator augmentations).

The asymmetry between Panels B and C is suggestive against a pure case-resolved-fast selection story: under symmetric selection on resolution speed, both pre-election dispositions would penalise equally.

The acquittal estimates serve as a falsification: if a pre-election conviction penalises through case-resolution selection (fast cases differ from slow ones in ways correlated with electoral viability) rather than through verdict content, then a pre-election acquittal should produce the same penalty as a pre-election conviction.

if a pre-election conviction were penalising candidates purely because fast-disposition cases differ from slow-disposition cases on unobservables that hurt electoral fortunes, then a pre-election acquittal would carry the same penalty.