The one clear case of substantive rejection is the court-structure reform (NOU 2020:11), reversed by a later government in an openly partisan dispute over centralisation—and even there most of the reform survived.
The one that I FIND! It might be that the rejections are there, but i cant find them.Also where did we find the evidence for this claim?
A reading of the parliamentary and legislative record of these reports suggests their low adoption reflects institutional friction rather than the government rejecting expert advice on its merits. In ministers' own answers to Stortinget questions, the stated reasons concern priority, timing, and consensus, not substance: asked why the revision of the Foundations Act (NOU 2016:21) had not advanced eight years after delivery, the responsible minister replied that she “must at all times prioritise which laws to revise” and that “the present Act functions well,” while calling the commission's proposals “good”; the long effort to consolidate work-injury compensation (NOU 2004:3) stalled, in successive ministers' words, because “the social partners have not managed to agree,” not because the reform was judged unsound.21 The clear exception is the court-structure reform (NOU 2020:11), enacted under one government and partly reversed by its successor in an openly partisan dispute over centralisation—a genuine political reversal, though even there most of the reform survived.
These are all anecdotes for which we have found the reasons for the "shelving". I think we should be briefer and less exlicit about the exact NOU, if anything, we should lists these reasons we have found, and then we can reference the specific NOU and the source document in a footnote. I want this to read as "we have checked why some of them are shelved, for some we did find these reasons, for other we found no reason, but 5.2. and Appendix A.3. showcase its hard for us to find any systematic reason. Should we add more analysis to show that these systematic reasons are negligble?
Length is itself a strong predictor of trimming (−7.8 percentage points per log-character),
This part of the sentence should be dropped unless we have a appendix analysis to showcase it.
This trim estimate, however, is sensitive to provision length, and I flag that directly rather than control it away.
This sentence is very strange, and i dont think it belongs. We could even skip it.
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.)
Can you check Prop. 62 L (2025-2026) ? Is that part of my data, and is that Prop L targeting the NOU in question?
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.
Det virker som om Norge har ratifisert Rotterdamreglene, men enda ikke implementert dem. No appraent reason
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.
This looks correct to me, according to the spørsmål in Stortinget
Full standardisation was not adopted; only a narrow part (standardised income-loss compensation for children) was enacted later (2015).
This looks correct to me. It was partly enacted, but not fully
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.)
Verbatim reasons: "For viktige spørsmåls del er utredningen avgitt med markerte dissenser. Utredningen var på høring med frist for uttalelse 1. desember 2004. I tiden før og etter denne datoen er det innkommet et større antall høringsuttalelser, til dels med omfattende merknader til de ulike spørsmål som er behandlet. Saken krever en grundig behandling, både juridisk/teknisk og politisk, før det vil bli avklart hvilket lovforslag Justisdepartementet vil fremme. "
Resulting §5 structure (each section = an answer to "when does the government reclaim authority?")
Okay, so i think we should change the set-up to instead be based on the theoretical predictions first. 5.1. has to be there, 5.2. is appendix at best, 5.3. we keep, 5.4. we keep, 5.5. we keep thinking about it, but its not the most important analysis right now, 5.6 has to be cimpletely redone, 5.7 for the future.
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.
Not sure what this means, but i dont think this is so necessary, since i think the theory-motivated analsysi came somewhat irrespective of this. So i trust those results, and also the labelling is more intuitive in the new analyses.
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.
To be fair, i thnk our strategy right now should just be to fland the result sections that is based on the theoretical framework. Then after that is finished, we could potenttially start thinking about supplementary anbalyses, such as lovdata counterfactual.
Maskin–Tirole (2004)
This is correct. See point 3 in the conclusion
lobbying section
I couldnt find this section? Are we talking about the same paper? Ie formal and real authority in org
4 — organized losers +3.1pp adopted (p=.011); distribution→FULL sharpens to −7.0pp once losers controlled (separable)
Shouldnt we also refer to Alesina and Tabellini here? Specifically, they make the claim that "From a perspective of economic efficiencty, politicians are preferable for tasks that have the following features:" "the stakes for organized interest groups are small, or the legal system is poorly designed so that corruption is widespread;"
I.e. isnt this the opposite of what we find? Or am i getting this wrong? Check the paper and add the citation if i am corret that these relate
Majone (1999)
I have read this, and think this can be used as an argument to explain the high implementation rate, and why its is so insulated from political changes in parliament, Specifically, this sentence i found good: "Both explanations - the reduction of decision-making costs and the blame-avoidance hypothesis - have merit, but they do not tell us why, at least in Europe, delegation to non-majoritarian institutions was rather infrequent in the past and is so popular now. The reason, I suggest, is that both approaches miss what is probably the main reason today for delegating policy-making powers to such institutions: the need to achieve credible policy commitments."
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.
I have read the intro, and to my understanding, this framing makes sense. However, one minor thing im wondring about is that they talk about the initiative of the agent to choose a project, which cannot be the case in this setting. Instead, the principal is choosing the project of the agent. Does that screw with the framing or make it more difficult?
how is law-making authority distributed between elected governments and the expert bodies they commission — and when does the government reclaim it?
An open question about this is the seleciton-issue. While we can argue that the government actually delegates authority to the expert body, the fact that they can appoint whomwever they want (although they dont do this as it would imply a loss of legitimacy), then you could argue that they do not delegate the authority, but rather just ask a commission for a specific conclusion. However, the commission might deviate from that still. So its not that clear, but i think theorticlly, this fact that there is front-end selection might destroy this argument. Is that fatal? Can we fix 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.
Delete this sentence. We will have to come up with such a sentence later, when we have more time to think about it.
, plausibly reflecting the COVID-delayed election and shorter follow-up window.
I am not sure about why this refects COVID-delayed election? Maybe just remove this reasoning completely and let us think about this after this version of the draft.
A Supplementary analyses
Some comments here: 1. In the compiled version of the paper, Appendix Table A5 does not fit into one page, which also makes the order of the Appendix tables and Figures come in the wrong order. Specifically, Table A5 comes before A2-A4. Fix this to fit A5 in the paper and also so that the Appendix Figures and Tables come in the correct order in the compiled version. 2. Make sure that we refer to all Appendix Figures and Tables in the main paper. If not, flag to me which places, and whether it makes sense to includes a reference to them.
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.
We already covered most of this in the paper, so cut this down a lot. Let the table do the talk, and then the text we had in the paper should do the talking about this table.
, taken from the project’s media database
Drop this part of the sentence.
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.
I think Appendix C delivers a strong and important analysis. However, I am not sure if this comes across like this in the current way we write this out. This part of the paragraph has to be written even clearer,potentially using more words if that is necessary to make this analysis more accessible to the reader.
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.
I like this whole paragraph a lot, but I think the two last sentences are a bit difficult I prefer the style to be direct and easy to understand. Also, the introdction of >= is somewhat weird. Espescially, since in fact we would have to look at the absolute values here. Can you fix this?
A decomposition of the Panel A coefficient by plaintiff identity (Panel F of Appendix Table A.5) sharpens this reading.
Dont refer to it as "Panel A coefficients", instead, be explicit about what the coefficients in Panel A measured.
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.
Change "court.-environment specification" to something else. This is the first time in the paper we have used this term, so i would prefer if we used terms more similar to what we did in the OLS section
Also, this sentence is incredibly long and very AI-like. Make the sentences shorter and skip the use of ";"
Abstract
In your answer to this comment, give me a summary of what parts of the Appendix you have removed (I have commented on which parts of the Appendix you should remove), and what each of these Appendices did.
This is so that I can give a summary to my co-author, so that he can decide whether or not he wants to re-include these analyses.
E Post-LASSO IV: sparsity diagnostics and alternative estimators
Remove Appendix E from this draft and any references we have to this Appendix and FiguresTables within this Appendix.
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.
Dont refer to it as "Panel A coefficients", instead, refer to it as what it actuually is: coefficienbts on association between filing and electoral outcomes.
The publicity caveat discussed at length in Section 4.3 also applies here.
INstead of referencing this, just add a short sentence or two about what the publicitiy caveat is.
; 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).
Drop this since we are skipping the Lasso and Appendix D from this dradft.
Predetermined politician-history controls enter Appendix Table D.1 as a precision-adjustment robustness, but do not enter the headline.
Drop since we are dropping Appendix D.
; the side-by-side comparison with the LASSO instrument is in Appendix Figure D.1.
Drop this sentence since we will drop Appendix D from this draft.
Appendix Table D.1 confirms that absorbing all nine controls in the second stage leaves the headline IV unchanged.
Drop this sentence since we will drop Appendix E from this draft.
e; alternative first-stage estimators (LASSO, Ridge, no-selection benchmark) are reported in Appendix E.
Drop this sentence, sincewe are going to remove Appendix E from this version.
Cross-estimator balance and selected-feature diagnostics for the alternative first-stage estimators are in Appendix E.
Remove this sentence since we are dropping Appendix D from this draft
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.
Make this easier. We dont have to explain what might the selection might be here. Instead, just say that the OLS might give us a null either because there is no real effect, or because of the selection. We use an judge IV to find the causal effect. The first part of this paragraph can be shorter.
Also, no need to reference the old section. Instead just say "results thus far" or something.
asdasd
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.
Drop this discussion completetly. It is relevant to refer to the per -office breakdown, but any discussion like this is over the top and should be deferred to either the Appendix or to a footnote. I think we should just skip this discussion for now and jkust commment on whether the cofficients for mayors/councilors are similar to our main results.
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.
This is very bad, and something we should remove from the paper. Instead, focus on saying something about each outcome, i.e. Running, elected, vote share, and choose one preferred specification to discuss the estimate. What does the estimate mean, is it stat sign, what is the interpretation, etc?
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.
This is too long. The most important thing here is to explain the results in Column (1), and why it differ from Column 2-4. And what controls we are introducting in Column (2)-(4) and then tell that the results are remarkably stable across these specifications, even in the most demanding one in Column 4. Also be specific on the estimates.
First-time / never-won candidates are excluded;
Again, do you mean first-time at the reference election? IN which case they have are never-won candidates. This makes this sentence very confusing. I dont get it.
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).
I think all of these can be dropped. This is just repetition from Section 3.3. Sample construction, Instead, this paragraph should be straight to the point, saying something like: To estimate the association between filing and electoral outcomes, we estimate:"
Then introduce the equations, and explain the variables, with emphasis on the variable of interest.
I also think it is better if we explain the equation for Panel A first, and then for Panel B. We could potentially split into two paragraphs. All variables should be explained, and all outcomes.
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).
Skip this. The variables should be defined AFTER we have introduced the equations 1 and 2, not before. Hence, any explanation of these variables should come later.
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.
Skip all of this. This belongs in the seciton where we define the sample (section 3.3.) and i think we already covered most of it there.
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
Simplify this. Could we explain the same thing without introducing notation?
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.
Drop these two sentences.
The same case-level structure, with additional randomisation prerequisites: non-missing court unit (vara) and stratum (judicial district × filing year) identifiers
Drop the use of the word "stratum". Be even clearer on the fact that all of these cases are randomly assigned.
The joint conviction–acquittal regression in Section 4.2 is estimated on this sample.
Drop this sentence.
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.
This reads too technical and AI-like. Make it very direct and shorter. What info do we need? If the only information we need is the reference ti Appendix Figure A.1., then leave it at that.
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.
Delete this info. It's not relevant.
This is the actuarial life-table estimator with administrative censoring.
Drop this sentence.
— the last year the current TJSP extract covers reliably —
We have previosuly said we have data until 2022. If we only have data until 2020, i dont see why we should include the 2020 election in this figure, as it would essentially not be part of every point along the x-axis from 1y, 2y, etc.
— mayors are exposed at roughly ten times the rate of councillors
Drop.
(these reflect prior public-service roles, ongoing investigations that crystallise into filings around election time, and cases naming the politician as a candidate)
make this shorter. I think its sufficient to say that these reflect prior public-service roles. If more information is needed we should put this in a footnote, potentially showing anecdotal evidence in what capacity the first-time elected poltician had this case filed against them. For example if they were working in the municipality before running for office,
The OLS evidence in Section 4.3 uses two samples drawn from this panel.
Honestly, i dont like this paragraph and the table. It is unclear what the sample is here, how it is constructed. Also, is this the case we end up using for the OLS-estimation? In which case i actually think it might make sense to change the structure.
Currently 3.3. is about linking judicial and electoral data with table 2, 3.4 about how common these cases are, and 4.1 about sample.
I think these three have a lot to do with eachother. For example, we could tlak about matching producedure, then show Figure 2 as a "first-glance on the data" and then introduce sample construction and table 2. Also, table 2 is currenlty ahrd to understand. We have to be very transparent about how the sample is constructed, what are the criteria for being included in the sample, etc. Currenlty i think we are doing a poor job on this. Im still unsure how we have constructed these samples.
The Filing-OLS sample (Panel A of Table 2) is a candidacy-grain sample of all incumbents at the 2008/2012/2016/2020
Again, shouldnt we skip the 2008 incumbents if our judicial data on filings start in 2012? Verify.
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
Is this really necessary, or can we skip this info for the intro? We hav kind of covered some of the results for the actquittal in the para above. Alsom, i dont like that we introduce the betas before we have defined them, althoiugh their self-explanatory in some sense.
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
very long sentence. Could we split it?
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
This sentence now reads rtoo long and complicated.
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.
Keep this in mind, but i dont think we have to justify this. We have consistently just used data from after 2012 election, so let's jus do this for this grpah as well and skip this long explanations?
unless there's some good reason to include all of this that i dont see tright now
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
How does sample size change for the two different samples?
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.
This is not in line with how the paper should be written. Specifically, it should be written as an econ-paper syle draft. Referncing my comments like this is wrong and should not be done. You should solve my comments and add the analysis to the paper.
Vara assignment + identifiable stratum.
Again, what does it mean? That the case was randomly assigned?
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.
What are the observstions we are missing on vote share? Are those missing values, why are they just not set to zero if this is the case? Is it because they decided to rerun but we do not know their vote share?
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).
How do we treat varas with few observartion? E.g. if we compute instrument based on 10 observations?
Also, im not sure what is the sensitivity to the 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.
But isnt the treatrment different. Acquittal could be a signal that the politician is clean, wheresa conviction that the politician is dirty, so we should expect different penalties
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.
I dont get this argument. An acquittal could rather be thought of as a "positive shock", i.e. the people can be pleseanlty surprised that the politician was "clean" after all, hence they might reward that. Whereas a conviction might give the negative effect.
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.
I dont really get this. I think it should be clearer and a easier read.