All issues (93)

The only information is 'decenas' of semi-structured interviews in four cities. Number of interviews, recruitment, dates, host profiles (single room vs whole home, income, tenure, ownership), interview guide and analytic procedure are not reported, so representativeness and analytic saturation cannot be judged.

Impact: Limits all empirical claims to 'illustrative' status.

No income data are presented for the claimed reduction of economic precarity, and the vignettes suggest hosts were already precarious (hosting to pay rent or avoid eviction), so hardship may cause hosting rather than hosting causing hardship. No comparison with non-hosts or pre-hosting conditions.

Impact: The causal 'trade-off' is plausible but not demonstrated.

'Todos los anfitriones' (p. 7) and 'la mayoría de anfitriones' (p. 17) are used without any frequency data from the interviews.

Impact: Generalisations should be read as 'many interviewees'.

Claim that retirees are the fastest-growing host profile and retired women the best rated has no source.

Impact: Peripheral to the argument but should be discounted.

The theoretical lens is laid out before the data and excerpts are chosen to illustrate it. Hosts who enjoy hosting, who use it sporadically, or for whom it reduced stress are not discussed (except the note that initial social motives fade).

Impact: Findings are best read as a theoretically informed interpretation rather than an inductive result.

Footnote 1 restricts the study to peer-to-peer hosts and acknowledges that multi-listing hosts control the market, yet the conclusion speaks of 'the Airbnb model' as built on precarious subjects.

Impact: The conclusion should be limited to peer-to-peer hosts.

'Externalities' is used for priced value-adding extras; the host's activities are called 'variable capital' and the home 'fixed capital' although no labour-power is purchased; surplus value 'for Airbnb' is not derived.

Impact: Terminological; the descriptive content of the typology survives.

Response-time categories are a platform metric not a measure of burden; the snapshot date is missing; the 'Otro' category (15-36%) is undefined; three of six cities are outside the interview sample.

Impact: Table is consistent with, but does not demonstrate, permanent connectivity.

US and Spanish cities are pooled and the post-2008 Spanish crisis framing is applied to all hosts without comparative discussion.

Impact: Minor.

The abstract concludes the model 'generates negative impacts on the economic sustainability of the city and its inhabitants', but no impact is measured and the conclusion states that a study of impacts on rents, supply and displacement 'would be necessary'.

Impact: The impact conclusion should be treated as a hypothesis.

Same 182-day calendar-availability rule as in Gil (2021): booked nights are not 'available', calendar defaults vary, so the rule is a noisy proxy for residential use. No sensitivity analysis.

Impact: Magnitude uncertain; the citywide direction is plausible.

The paper asserts that all multi-listing hosts are professionals not hosting in their own residence, yet 44.5% of listings in the 2-5 band are private rooms. Hosts with several rooms in their own home would be misclassified.

Impact: Concentration findings stand; 'professional' label overstated for the 2-5 band.

Growth is reconstructed from host registration dates for listings active at scrape time (acknowledged in fn. 4). This omits exited listings and back-dates listings added later by long-standing hosts, and it classifies past listings using current availability. The 2017-vs-now comparison relies on an earlier paper's scrape whose comparability is not documented.

Impact: Temporal claims are weaker than the cross-sectional ones.

Central commercial share 80.07% vs city average 75.7% is a 4.4-point gap, not 'nearly 10 points' (the gap to the rest of the city is 8.4).

Impact: Presentational; direction unchanged.

The date of the main dataset is never given. The conclusion says over 50% of supply 'has been' in the Central District, while the current figure is 47.78%.

Impact: Minor.

The conclusion lists reduced rental supply, rent pressure, neighbourhood transformation and displacement as effects of the model, but the paper presents no rent trends, eviction/displacement or conversion data for Valencia; these are inferred from literature on other cities.

Impact: These conclusions should be read as hypotheses consistent with the indicators.

The p2p/commercial split and the 'cannot be habitual residence' inference rest on forward calendar availability, which excludes already-booked nights and reflects host calendar settings rather than actual use. Bias direction is ambiguous, so the 'most lenient possible' characterisation is not established. No sensitivity analysis (e.g. 90- or 120-day thresholds, or reviews-based activity).

Impact: Magnitudes uncertain; direction likely robust given the size of the gap.

Uniform 70 m2 size, asking rents from Idealista, list prices, district-average occupancy applied uniformly, 20% cost deduction, no platform fees/taxes/licence/furnishing costs. The author argues all choices are conservative, but list prices and omitted costs bias upward. No sensitivity ranges are reported and the averaging unit is unclear.

Impact: Existence of a positive gap is credible; the €500-1,200 magnitude is uncertain.

Entire-home listings are divided by the (undated) INE rental stock. Listings may come from owner-occupied, second or previously vacant homes, may be duplicated, or be in purpose-built tourist apartments; thus the ratio is not a measure of units removed from long-term rental.

Impact: Weakens the step from exposure to impact.

(a) 7,654 − 451 − 46 = 7,157, not the 7,203 analysed (7,203 = 7,654 − 451 only; the 46 long-stay listings appear not to have been removed, or overlap with inactive ones). (b) p2p nights are reported as 11.8% / commercial 88.2% on p. 10, but the reported counts give 10.87% / 89.13% (the conclusion uses 10.87%). (c) p2p listings given as 24.19% on p. 11 vs 24.23% elsewhere. (d) Single-listing hosts 71.91% vs 71.66% computed from counts. (e) Hosts with 6+ listings hold 23.4% of listings, described as 'casi un tercio'. (f) >20-listing hosts: 9.16% not 9.14%.

Impact: None on direction of conclusions; indicates limited proofreading.

Concentration is measured per host account; management companies may use several accounts and single accounts may represent many owners. The bias likely understates concentration among operators but overstates concentration of ownership.

Impact: Qualifies interpretation of 'who' controls supply.

Revenue is computed from availability, district occupancy and list price, so cross-host dispersion is largely mechanical (number of listings x availability). The step from revenue concentration to 'widening social inequality' needs information on who the hosts are.

Impact: Concentration finding stands; inequality interpretation is an extrapolation.

The boom is attributed to the package because it followed it. Concurrent drivers acknowledged elsewhere in the paper (QE, record-low rates, global liquidity, SAREB, bank restructuring, economic recovery) are not weighed, and no comparison case is used (e.g. countries adopting REIT regimes without LAU changes or privatizations).

Impact: The package plausibly contributed; its decisive role is not demonstrated.

Strategic coordination and design intent are asserted ('wisely coordinate', 'designed to') on the basis of co-occurrence and single-party control, without primary documentary evidence; the stated official rationales are dismissed rather than assessed.

Impact: The 'package' is an interpretive construct more than a documented plan.

(a) Row differences sum to €17,654,238 (= 200,726,431 − 183,072,193), not the €17,799,057 reported; per-home total is €6,015, not €5,394. (b) The 'average selling price' column contains totals, and every municipality's implied price per home is exactly €68,391 — i.e. a uniform pro-rata allocation, so municipal differences reflect only construction cost. (c) The table compares price with historical construction cost, not market value, so it cannot show 'below market price'; overall the sale exceeded cost.

Impact: Below-market claim rests on court findings, not on this table.

Many quantitative claims (fund acquisitions, Blackstone portfolio, revaluation gains) and court findings are cited through news media rather than primary documents.

Impact: Acceptable for context; reduces verifiability.

The paper states profits must be distributed to shareholders and then that SOCIMIs 'do not pay tax on non-distributed dividends' and that distributed dividends are not taxed 'as other companies do'; the description of where taxation falls is unclear.

Impact: Minor.

The paper's third research question (contribution to activism) is answered mainly with directors' statements and six activist consultations; there are no audience figures for the films judged most successful, and no testimony from branches that allegedly learned from Seven Days.

Impact: Typology stands; efficacy rankings are impressionistic.

The conclusion states the films 'evince' that the crisis was politically driven by neoliberal decisions; the films present this interpretation but are not evidence for it.

Impact: Rhetorical.

'On average 80,000 evictions per year 2009-2015' vs the paper's own footnote (40,740 repossessions in 2011, 64,902 in 2015, ~80% homes) and vs 409,000 evictions 2009-2018 in Gil & Martínez (state-led paper).

Impact: Background only.

Bankia and Blackstone are chosen as the firms that 'best illustrate' each period; with N = 2 and no within-period variation or counter-cases, the claim that political-economy cycles 'essentially define' protest dynamics cannot be distinguished from learning, opportunity structures or tenure composition.

Impact: Periodisation is a plausible heuristic, not a demonstrated determinant.

Bank protocols, reputational damage and 'halting' Blackstone are attributed to campaigns based on activist testimony and press; rival explanations (regulators, courts, bailout conditions, market cycle) and magnitudes are not assessed; the proposed media-based reputation indicator is not operationalised.

Impact: Documented local wins; broader effects uncertain.

€4bn across 87 card holders implies ≈€46m each; the figure likely duplicates the €4bn returned to preferential-share holders cited a few lines earlier.

Impact: Factual slip; does not alter the argument.

'Even below construction costs' conflicts with the IVIMA table in the authors' companion paper (sale exceeded cost overall). Minor differences also in unit counts (1,860 vs 1,861) and rent increases (40% vs 50%).

Impact: Background.

The 1,796 listings / 73.61% estimate and the Idealista counts are presented without explaining identification of former tourist units, dates, geography or extraction method.

Impact: The only empirical anchors of the paper cannot be assessed.

Professionalisation (small managers expelled), contract practices, and demand shift to urban roamers are stated as findings ('as the article has shown') but no supporting data are shown.

Impact: These are hypotheses for future research rather than results.

The abstract says the paper examines shifts in 'the type of demand', but no demand data are analysed; the abstract's claim that hedge funds favoured touristification is also not developed.

Impact: Editorial.

What distinguishes 'assetization' from rent-gap-driven touristification (liquidity, capital switching, investor ownership, asset-class treatment) is not measured: the data are listing-level only, with no ownership, transaction or capital-flow information. Hence the empirical section cannot adjudicate between the proposed concept and rival framings, and 'greater explanatory power' is asserted rather than demonstrated.

Impact: The concept remains a plausible theoretical proposal; the Valencia case illustrates but does not test it.

The 9,047 figure assumes every high-availability entire home displaced a tenant household; it is explicitly an estimate on p. 13 ('are believed to', 'are thought to') but becomes 'a minimum of 9,047 residents' in the discussion. The same 'at least' framing is applied to the supply-reduction figures, which rest on the assumption that multi-host listings were withdrawn from residential rental.

Impact: Headline displacement numbers should be read as upper-bound scenarios.

Rent increases are co-temporal only (and Ciutat Vella ranked 4th), and livability effects are inferred from capacity ratios; both are then stated as outcomes ('As a result, STRs ... increase residential rental prices'; 'does not deteriorate community livability').

Impact: These conclusions are hypotheses consistent with the data.

Gil (2021) used price x available days x occupancy − 20% and found €500-1,200/month; this paper uses price x occupancy − 15% commission − 20% and finds €497-958/month, without noting the change or reconciling results. Key assumptions (70 m2, asking rents, list prices) are unchanged and untested.

Impact: Magnitude uncertain; a positive gap likely.

'Occupancy rate' is used both for booked-night share (AirDNA) and for maximum guests per bedroom; the latter is compared with average household size (2.47) as if it were actual occupants. Also '40% / 30% / 20%' of listings by guests per bedroom sum to 90%.

Impact: Density differences are suggestive only.

Sample arithmetic (7,654 − 451 − 46 ≠ 7,203) and the 71.91% single-host share (should be 71.66%) are repeated from Gil (2021). Also 3,663 homes vs 74.75% x 4,920 = 3,678.

Impact: None on conclusions.

Band distributions are correlated with an overall distribution that includes them; no n, test or p-values are given; the pattern is not monotonic.

Impact: Weakens a secondary claim; the Ciutat Vella overrepresentation may still hold.

Revenue and 'yield' are modelled from district occupancy and list price; impact on the residential market is inferred, not measured. Over-representation units (percent vs points) are ambiguous.

Impact: Minor.

'It is therefore impossible for STR-induced rent gaps to emerge under a strict housing regulation' is an unqualified deduction; the cited pandemic evidence is in tension with other corpus papers that report some STR-to-residential switching.

Impact: Recommendation direction reasonable; certainty overstated.

'Hardest hit and most exploited' and 'more prone/more frequently targeted' are not supported by any comparison of outcomes across groups; the study's data are about PAH participants only.

Impact: Plausible claims presented as findings.

Survey items report gender and migrant shares separately and as estimates by group representatives; the intersection 'migrant women' — the paper's central subject — is never quantified.

Impact: Centrality of migrant women (vs women or migrants generally) rests on qualitative material.

55 interviews over seven years in nine cities, but no breakdown by gender, origin, role or tenure; only ~7 interviewees are quoted; no indication of how prevalent each theme was.

Impact: Limits assessment of representativeness of the empowerment narratives.

The claim that wide mobilisation is necessary for immediate success, and that other movements lack immediate goals, are not examined against contrasting cases.

Impact: Interpretive.

Both authors are union members and spokespeople evaluating their own organisations' impact. Positionality is disclosed, but there is no reflexive treatment of bias, no interviews with legislators/ministries/landlord organisations, and key counterfactual claims rely on unnamed ministers.

Impact: Causal attributions should be read as informed participant accounts.

Coalition agreement commitments, partisan competition, COVID-era policy diffusion (eviction moratoria internationally), budget bargaining and the votes of non-left parties are not systematically considered. The 2018 decree's defeat required a majority against, including parties outside the left bloc.

Impact: Union contribution is plausible; 'key factor' status not established.

Effects on 'urban accumulation', 'hegemonic crisis' and 'crises of representation' are inferred from individual episodes (one REIT exit, municipal adoption of rent control, Berlin referendum vote blocs).

Impact: Speculative conclusions.

'Surveys show strong support' for rent control, '140,000 households protected', union growth — no sources or data given.

Impact: Minor for the main argument.

The PAH activity list skips item 4; a sentence on the 2023 law apparently inverts its meaning ('mentions promoting social housing for rent, but makes it compulsory for the state to increase the budget', presumably 'does not make it compulsory').

Impact: Editorial.

Arguing that the counterproductive claim 'loses force' because the unregulated market supplies little affordable housing conflates the level of supply with the marginal effect of regulation on it.

Impact: Weakens one strand of the rebuttal; the case-by-case conclusion remains reasonable.

Opponents' arguments are tested rigorously while evidence unfavourable to the authors' position (e.g. quality deterioration found by most studies per Kholodilin) is countered with an older critique; the monopoly-rent claim is asserted strongly.

Impact: Tone of advocacy; conclusions still broadly defensible.

Same arguments across measures are taken as evidence of entrenched beliefs, though measures share the features that trigger those objections.

Impact: Minor.

The pension-fund rebuttal concerns Spanish savers only, whereas the contested claim concerned 'millions of individual citizens' in general; foreign pension capital is acknowledged to be significant.

Impact: Minor.

The text states non-corporate landlords are mostly multi-property, yet Table 1 shows 79% own one dwelling; what is true is that 60.3% of dwellings belong to multi-owners. The conclusion then asserts this holds for 'Spain's rental units' using only Barcelona data.

Impact: The concentration argument survives in its dwelling-share form, for Barcelona.

Quotes are chosen to illustrate the myth; no corpus, selection rule, frequency count or counter-examples (e.g. politicians distinguishing small landlords from large holders — Rufián's quote actually does this).

Impact: Shows the myth exists, not how dominant it is.

Discourses are said to be deployed 'deliberately' and 'with the aim of' preserving class interests; intent is inferred from content and beneficiaries. The paper concedes that activists and statistical offices also use the same categories, which weakens a purely interest-driven explanation.

Impact: The hegemony reading is plausible but not demonstrated.

Groups are based on a landlord's total annual rent received, which conflates rent per dwelling, number of dwellings and months let; index-based control depends on each dwelling's rent relative to the local index.

Impact: The 'low-rent landlords unaffected' inference is unsupported.

'92% of rented housing is owned by private individuals' is a statement about legal form that the authors do not dispute; the myth lies in equating individuals with small/vulnerable owners. The text sometimes blurs the two (e.g. 'all assert that 85%-95% of the rental market is controlled by private individuals who are small-scale landlords').

Impact: Rhetorical overreach.

It is not explicit whether Table 1 covers natural persons only (as the text implies) or all landlords including companies; this matters for the >15 group (24.1% of dwellings).

Impact: Could change the interpretation of top concentration.

The paper does not state whether 'landlord households' in LCS are identified by housing rental income specifically or by any property/land rental income.

Impact: Likely small given convergence with other sources.

Tenant at-risk-of-poverty rate is 30.16% in the results and 36.28% in the conclusions; landlord rate 6.47% vs 6.48%. The 36.28% figure coincides with the LCS-2021 estimate (36.3%) published in Vidal, Gil & Martínez (2024), suggesting the conclusion was not updated after switching to LCS 2023.

Impact: Does not alter the contrast.

The cycle of contention is attributed to GCLs, but tenant unions also confront small and medium landlords and general rent inflation; no comparison isolates GCLs' role. 'Endemic' rogue practices generalise from cases.

Impact: Framing claim plausible but not demonstrated.

Acknowledged by the authors; contributions come from politically engaged scholars studying visible conflicts, which favours cases where contention occurred.

Impact: Limits generalisability; acknowledged.

Per the methodological note, EFF 'inmuebles' include garages, warehouses, shops, offices and hotels; Catastro urban units likewise include parking spaces and storage rooms. A household owning its flat and a garage is a 'multi-owner'. The report nonetheless interprets results as housing concentration ('el problema de la vivienda'). No residential-only breakdown is shown.

Impact: Multi-ownership levels and possibly trends are not interpretable as housing concentration without a dwellings-only analysis.

The executive summary says households living in their own home fell from 79% to 63.9%, but 'propietario' excludes owner-occupiers who receive rent (classified as 'caseros'). With footnote 1, owner-occupancy in 2022 is ≈72%. Part of the fall in 'owners' is owners becoming landlords, not losing ownership.

Impact: Overstates the decline of owner-occupation by roughly 8 points.

Changes in the size of portfolio bands between two cross-sections are read as faster growth for households with larger initial portfolios. Band membership changes over time; panel data would be needed.

Impact: The 'rich get richer' mechanism is plausible but not shown.

Household count grew ~11% (implied 17.3M → 19.1M), with new households (young, immigrant) typically non-owners; ageing and inheritance increase multi-ownership mechanically. Neither demographic composition nor age-specific rates are analysed.

Impact: Polarisation may be partly compositional.

Catastro (holders, 2008-2025) and EFF (households, 2008-2022) are combined in single summary statements (e.g. point 3 mixes Catastro band growth with EFF property counts). EFF-implied growth of household-held properties (+6.2M) is three times the '2 million' Catastro stock growth used in the conclusion. The multi-owner 'majority' holds in Catastro (51.7%) but not in EFF (47.6%).

Impact: Readers cannot tell which source supports which number.

EFF estimates for small groups (>10 properties, 4-5 properties) are reported to the unit (e.g. 625,883) without confidence intervals.

Impact: Spurious precision for small groups.

Multi-landlord status is 'determined by aggregating and counting unique cadastral references linked to each landlord household in the Panel's real-estate module'. Garages, storage rooms and the landlord's own residence each have distinct cadastral references. Unless counting is restricted to dwellings actually let (not stated), landlords letting one flat could be classified as multi-landlords. Co-owned dwellings may be counted once per co-owning household.

Impact: Could materially inflate the 52.8% headline; direction and size unknown from the report.

The methodological note states that municipal figures reflect the portfolios of landlords who file taxes in the city, wherever their dwellings are. The executive summary and section 1 nevertheless describe them as the share of each city's rental market controlled by multi-landlords and infer a link with local price pressure.

Impact: City comparisons cannot support claims about local markets.

The ~60% figure groups private multi-landlords, companies and ~300,000 public/social dwellings, and the synthesis describes the whole as multi-landlords concentrating the market. Public landlords are not the object of the 'concentration' critique. Excluding them, single landlords hold 43.4% and private multi + corporate 56.6%.

Impact: The 60/40 headline mixes conceptually different actors.

Tax data capture only declared residential lettings in the common fiscal territory. The report's own figure of 20.2% tenant households (with the companion report's ~19.1M households) implies ~3.9M renting households vs the 3.09M dwellings counted. Who owns the undeclared segment is unknown, so shares may be biased.

Impact: Shares apply to the declared market only.

The single-landlord share moves from ~49.0% to 47.2% in seven years. Growth by category is read as growth by incumbents with several dwellings, though landlords change category. Formalisation of previously undeclared lettings could also differ by landlord type.

Impact: Direction credible, magnitude small; the 'clear trend' language is strong.

Section 1 text says '64.9% of landlords are multi-landlords' while the chart and summary report '% of rented dwellings'. These are different quantities (the landlord share is necessarily lower).

Impact: Confusing; probably a wording error.

Tenure groups are defined by property ownership, which is most of household wealth, so they differ in wealth largely by construction; comparing ranges of medians across groups of very different sizes (small multi-landlord group vs broad age bands) is not a test of 'which divides more'. Causality from tenure to wealth is asserted although low wealth also causes tenancy.

Impact: The 'tenure not age' conclusion is not established by the analysis shown.

No comparison with other determinants (education, employment, financial wealth, inheritance). The executive summary says 'el principal eje', the conclusion 'uno de los principales ejes'.

Impact: Headline should read 'a major axis'.

Medians for small groups (multi-landlords with 3 or 4+ dwellings; under-35 household heads per wave) are reported without n or confidence intervals, despite the EFF providing the means to compute them.

Impact: Precision of extreme-group figures and of the youth-ownership collapse unknown.

Delayed emancipation changes who appears as an under-35 household; selection into household formation and immigration could account for part of the ownership drop.

Impact: The 'exclusion' interpretation may overstate the change for the cohort as a whole.

Rent flows are not traced between specific tenants and landlords; some tenants rent from corporate/public landlords; landlords' income includes rent received.

Impact: Direction plausible; the statement is appropriately hedged in the conclusion.

Top-share change uses 2002, Gini change uses 2005 (series minimum). From 2002, the Gini rise is +15% not +18%.

Impact: Small overstatement.

OLS on quarterly levels of strongly trending series (listings, prices) without detrending, differencing, autocorrelation-robust errors or unit-root checks risks spurious significance; four correlated predictors (rent gap is a function of price/m2) with 24 observations; the text speaks of 'growth' while models use levels. The authors flag small N but not these issues.

Impact: Regression results cannot discriminate among H1-H3 with confidence.

No regulation variable (dummies for Law 11/2020 in force, Law 12/2023, Catalan application in 2024) enters any model; H1 support is inferred from a negative rent-gap coefficient and descriptive timing. An interrupted time-series or difference-in-differences vs Madrid/Málaga would be the natural test.

Impact: Barcelona's regulatory story rests on descriptive timing (which is actually quite persuasive) rather than the regression.

Reverse causality (MTR supply growth lowers MTR prices; LTR listing scarcity raises LTR asking prices) and mis-measured incentive (the capped legal rent, not asking LTR rent, is the landlord's alternative under control) can produce the negative sign. Evasion of controls is a form of profit maximisation, so 'rules out profit maximisation' is a false dichotomy.

Impact: The H1 conclusion may be right, but not for the reason given.

MTRs turn over (and are advertised) more often than LTRs; longer LTR leases and rent control reduce LTR vacancies reaching the platform; landlords may fill controlled units off-platform. Listing shares and leads-per-listing therefore exaggerate shifts in the underlying stock and in competition.

Impact: Direction credible; magnitudes overstated.

Barcelona's rent gap fell 36.5 points from its Dec-2021 peak, or 17.2 points since 2019 — described as 'a compression of 17 percentage points in three years'. Madrid's 17.97% is the MTR/residential ratio, not 'of total listings' (≈15.2% of total). Simple-regression β (−0.94) and multiple-regression coefficient (−140.8) appear to be on different scales without explanation.

Impact: Minor.

The introduction says transnational demand is not significant 'in any of the three cities', but simple regressions are significant in Madrid and Málaga (only multivariate models are null). Two references are printed with '[to be confirmed]' placeholders.

Impact: Editorial; the conclusion itself is nuanced.