One of eight open-access SAGE papers · all eight
A new model of social class from the Great British Class Survey
Savage et al. 2013. A New Model of Social Class? Findings from the BBC’s Great British Class Survey Experiment. Sociology, 10.1177/0038038513481128. CC BY, cited by 1,300 works (17 October 2026).
How to read these graphs
A discourse graph breaks a piece of research into typed one-sentence nodes and draws how they bear on one another. The grammar is that of Discourse Graphs (Chan and Akamatsu). Read each graph left to right: a question, the experiments that addressed it, the results they produced, and the hypothesis every result is drawn against.
- QUE Question
- What the work set out to answer.
- HYP Hypothesis
- The answer the authors expected. Every result earns one edge against it.
- EXP Experiment
- One attempt at the question: a trial arm, an assay, a survey, an analysis.
- RES Result
- One finding from an experiment, with where in the source it comes from.
- ISS Issue
- An open question or untried branch the work leaves for someone else.
- addresses
- An experiment addresses the question.
- produces
- An experiment produces a result.
- supports
- A positive result that backs the hypothesis.
- opposes
- A negative result that counts as evidence against the hypothesis, or a refutation of an earlier claim.
- informs
- A partial or mixed result that bears on the hypothesis without settling it.
- consistent with
- A negative or inconclusive result that does not count either way: no positive control passed, or there is no sensitivity or power statement, so the absence of an effect cannot be told from a measurement that failed.
- relation
- A thin dotted line: a link the source itself states between two experiments, such as one being derived from another.
A dashed box marks a result the rule above counts as uninformative, or an issue. In the drawing, click a node to jump to its text below.
Seven-class model from the BBC Great British Class Survey (Sociology, 2013)
Read left to right. The question (QUE) is addressed by 4 experiments (EXP), each producing results (RES), and each result bears on the hypothesis (HYP). 5 support it, 0 oppose it, 6 inform it. Issues (ISS) hang below: what the paper leaves open.
HYP, in the authors’ words (Introduction): “This article contributes to this current by elaborating a new model of social class which shows how measures of economic, cultural and social capital can be combined to provide a powerful way of mapping contemporary class divisions in the UK.”
- supports positive finding
- opposes a negative with a control and a stated sensitivity, or a failed replication
- informs bears on the question without deciding the hypothesis
- thin grey a relation between two experiments
| Node | Text | Type | Outcome | Edge |
|---|---|---|---|---|
| EXP | BBC Lab UK web survey (GBCS) on economic, cultural and social capital, launched 26 January 2011; 161,400 complete surveys by July 2011 The web survey produced an unprecedentedly large and granular dataset but was strongly skewed towards well-educated groups and could not be reweighted to be representative. | web survey (self-selected) | partial | |
| RES | The 161,400-respondent web sample over-represented professionals and under-represented manual workers: traditional professionals 17.9% vs 4.8% nationally (ratio 3.7), routine workers 3.2% vs 14.5%. Table 1: Senior manager 13.0 vs 6.3 (ratio 2.1); Traditional professional 17.9 vs 4.8 (3.7); Modern professional 31.5 vs 18.1 (1.7); Technical craft worker 2.4 vs 10.6 (0.2); Semi-routine worker 4.9 vs 15.3 (0.3); Routine worker 3.2 vs 14.5 (0.2); n = 161,400 web, 1026 national The Great British Class Survey (GBCS); Table 1 · “the GBCS web survey suffered from a strong selection bias, with respondents being predominantly drawn from the well-educated social groups” | partialinformative | informs HYP | |
| RES | Simple weighting of the web sample to national proportions was not possible because GBCS respondents from routine classes were unrepresentative of their peers; GBCS alone cannot give a class model. No numeric effect reported; comparison with the Culture, Class, Distinction (Bennett et al., 2008) study; GBCS mean household income £52,766 vs GfK £31,856 (Table 4); GBCS mean status score of contacts 50.2 vs GfK 40.9 (Table 2) The Great British Class Survey (GBCS); Tables 2 and 4; footnote 11 · “not possible to simply weight the GBCS to deal with these skews because the GBCS respondents from routine classes turn out to be highly unrepresentative” | negative-not-achievableinformative | informs HYP | |
| EXP | Nationally representative face-to-face quota-sample survey by GfK with identical questions, April 2011; 1026 respondents, commissioned to correct the web survey's skew The GfK survey was judged nationally representative and supplied the baseline measures of social, cultural and economic capital on which the class model was built. | nationally representative sample survey (quota sampling) | positive | |
| RES | In the 1026-respondent GfK sample the average respondent knew someone in 13.3 of 34 valid occupations, with mean contact status 40.9, mean household income £31,856 and mean savings £20,084. Table 2 (GfK): number of occupations reported mean 13.3 (σ 7.1), mean status score 40.9 (σ 9.7), range 62.4 (σ 17.9); Table 3 (GfK): high culture score 10.3 (σ 4.9), emerging culture score 13.5 (σ 6.3); Table 4 (GfK): household income £31,856 (σ £31,027), property value £126,706, savings £20,084; n = 1026 The Great British Class Survey (GBCS); Measuring Social, Cultural and Economic Capital; Tables 2-4 · “This survey, with 1026 respondents, was conducted using quota sampling methods by the well-known survey firm GfK in April 2011.” | positiveinformative | informs HYP | |
| EXP | Specific multiple correspondence analysis (MCA) of 27 cultural taste variables on the GfK sample (n = 1026) to derive measures of cultural capital inductively The MCA separated cultural engagement from disengagement on the first axis and highbrow from 'emerging' culture on the second, yielding two cultural capital scores. | multiple correspondence analysis | positive | |
| RES | MCA on 27 cultural variables gave a first axis of engaged vs disengaged and a second axis of highbrow vs emerging culture, producing a highbrow score (max 30) and an emerging score (max 32). 27 cultural variables; highbrow cultural capital score maximum = 30; emerging cultural capital score maximum = 32; no eigenvalues or variance explained reported; n = 1026 (GfK) Cultural Capital; Figures 1-2; Table 3 · “there are now two main types of cultural capital: that associated with highbrow taste, and what we term ‘emerging’ cultural capital” | positiveinformative | informs HYP | |
| EXP | Latent class (latent profile) analysis on six standardised capital measures; GfK cases at original weights plus 161,400 GBCS cases weighted 1/161400 each The BIC was minimised at seven classes; the model is derived from the representative GfK survey and then used to classify all GBCS web respondents. | latent class analysis | positive | |
| RES | The Bayesian Information Criterion was minimised at seven clusters (BIC = 12991.8), adopted as the class solution. BIC = 12991.8 at seven clusters; six input variables (mean status score of contacts, number of contacts, highbrow cultural capital, emerging cultural capital, income, assets); GfK n = 1026 at original weights, GBCS n = 161,400 at 1/161400 each A Latent Class Analysis of Social Class · “The Bayesian Information Criterion (BIC) is minimised at seven clusters (BIC = 12991.8): we therefore take this as our solution.” | positiveinformative | supports HYP | |
| RES | Class 1, Elite: 6% of GfK and 22% of GBCS respondents, with mean household income £89,082, savings £142,458, house value £325,000, highest highbrow cultural capital (16.9) and 56% graduates. Table 5: 6% GfK, 22% GBCS; Table 6: household income £89,082, savings £142,458, house value £325,000, social contact score 50.1, contact number 16.2, highbrow 16.9, emerging 14.4; Table 7: mean age 57, 56% graduates, 52% from professional or senior management families; Table 8: 60.5% of chief executive officers (N 4,953) in this class Class 1: Elite; Tables 5-8 · “Their mean household income is £89k, almost double that of the next highest class, and the average house price is £325k” | positiveinformative | supports HYP | |
| RES | Class 2, Established middle class: 25% GfK / 43% GBCS, income £47,184, 17.0 contacts; Class 3, Technical middle class: 6% GfK / 10% GBCS, income £37,428, savings £65,844, only 3.6 contacts. Table 5: established middle class 25% GfK, 43% GBCS; technical middle class 6% GfK, 10% GBCS. Table 6: established middle class income £47,184, savings £26,090, house £176,834, contact score 45.3, contact number 17.0, highbrow 13.7, emerging 16.5; technical middle class income £37,428, savings £65,844, house £163,362, contact score 53.5, contact number 3.6, highbrow 9.2, emerging 11.4. Table 7: technical middle class 59% female, 26% graduates Class 2: Established middle class; Class 3: Technical middle class; Tables 5-7 · “the lowest number of social contacts of any of the classes (an astonishingly low average of four out of 34 possible contacts, compared to 17” | positiveinformative | supports HYP | |
| RES | Class 4, New affluent workers: 15% GfK / 6% GBCS, income £29,252, emerging cultural capital 14.8 vs highbrow 6.9; Class 5, Traditional working class: 14% GfK / 2% GBCS, income £13,305, mean age 66. Table 5: new affluent workers 15% GfK, 6% GBCS; traditional working class 14% GfK, 2% GBCS. Table 6: new affluent workers income £29,252, savings £4,918, house £128,639, contact number 16.9, highbrow 6.9, emerging 14.8; traditional working class income £13,305, savings £9,500, house £127,174, contact number 9.8, highbrow 10.8, emerging 6.5. Table 7: new affluent workers mean age 44, 43% female, 11% graduates; traditional working class mean age 66, 62% female, 11% graduates Class 4: New affluent workers; Class 5: Traditional working class; Tables 5-7 · “They actually form a significant part of the population, at 15 per cent, but cannot easily be identified as either middle or working class.” | positiveinformative | supports HYP | |
| RES | Class 6, Emergent service workers: 19% GfK / 17% GBCS, income £21,048, highest emerging cultural capital (17.5), mean age 34; Class 7, Precariat: 15% GfK / <1% GBCS, income £8,253, 6.7 contacts. Table 5: emergent service workers 19% GfK, 17% GBCS; precariat 15% GfK, <1% GBCS. Table 6: emergent service workers income £21,048, savings £1,138, house £17,968, contact score 38.3, contact number 14.8, highbrow 9.6, emerging 17.5; precariat income £8,253, savings £793, house £26,948, contact score 29.9, contact number 6.7, highbrow 6.0, emerging 8.4. Table 7: emergent service workers mean age 34, 21% ethnic minority, 19% graduates; precariat mean age 50, 3% graduates, 5% from professional families Class 6: Emergent service workers; Class 7: Precariat; Tables 5-7 · “the most deprived of the classes that we have identified, on all measures, yet they form a relatively large social class, with 15 per cent” | positiveinformative | supports HYP | |
| RES | Only two of the seven classes (established middle class and traditional working class) match conventional middle/working class models, together covering 39% of the national population. 39 per cent of the national population in established middle class (25%) plus traditional working class (14%); Table 5, GfK Conclusion (fourth point); Table 5 · “only 39 per cent of the national population fall into these two classes, which conform most closely to these middle and working-class sociological stereotypes” | positiveinformative | informs HYP | |
| RES | Apart from chief executive officers (60.5% of 4,953 in the elite), no specific occupation showed a clear affiliation with any latent class; occupational membership is spread unevenly across classes. Table 8: chief executive officers 60.5% in elite (N 4,953); established middle class occupations never more than 50 per cent more likely to be in that class than the GBCS as a whole; aircraft pilots 78 per cent more likely to be technical middle class; GBCS n = 161,400 Conclusion (first point); Table 8; Class 2 and Class 3 sections · “Leaving aside the particular case of chief executive officers who are predominantly located in our ‘elite’, we have found no clear affiliation between specific occupations” | partialinformative | informs HYP |
- ISS Whether 'emerging' cultural capital is a robust form of capital that competes with established forms is unresolved and said to warrant further investigation. (open-question · Conclusion; footnote 9)proposed experiment
- ISS Household measures of income, savings and house value obscure within-household divisions, so relationships between gender and class are not fully registered. (open-question · Economic Capital; Conclusion)proposed experiment
- ISS GBCS respondents in routine and semi-routine jobs are untypical of their peers, so extrapolating occupational profiles to lower social classes needs caution. (open-question · footnote 11; The Great British Class Survey (GBCS))proposed experiment
- ISS Fuller accounts of educational and occupational profiles (including specific universities) and cross-fertilisation with qualitative research are deferred to future work. (next-step · Conclusion; footnote 12)proposed experiment
Extraction notes: Author-flagged skew of the web sample: stated in the GBCS section ('strong selection bias, with respondents being predominantly drawn from the well-educated social groups'; the BBC journalist's 'typical BBC news audience' remark; 'GBCS alone cannot be used to derive a representative model of class'), quantified in Table 1, repeated in footnote 11 (routine and semi-routine GBCS respondents untypical of peers; comparisons between professional/managerial occupations and between universities are said to be robust), and handled in the LCA by weighting each GBCS case at 1/161400. Table 2 and 4 contrasts (GBCS mean contact status 50.2 vs GfK 40.9; income £52,766 vs £31,856) also show the skew but the authors do not explicitly label them as such; that reading is mine. Self-inconsistencies in the text: (a) GBCS percentages per class differ between Table 5 and Table 8 and the prose: technical middle class 10% (Table 5) vs 9.46 (Table 8); new affluent workers 6% (Table 5) vs 5.8 (Table 8) vs 'only 5.4 per cent' (Class 4 prose); elite 22 vs 21.8; established middle class 43 vs 43.3; emergent service workers 17 vs 17.3; precariat <1 vs 0.7. (b) Traditional working class mean age is 66 in Table 7 but 'an average age of 65' in the Conclusion. (c) Prose rounds Table 6 values (technical middle class 'four' contacts vs 3.6; traditional working class '10' vs 9.8; precariat 'seven' vs 6.7). (d) Social capital question covers 37 occupations but 34 'valid' ones are scored (students, never worked, aristocrats lack CAMSIS scores). (e) Table 6 gives emergent service workers a house value of £17,968, lower than the precariat's £26,948; the prose only says they are 'likely to rent', so this is not explained. (f) Table 1 is described as occupational categories from the NS-SEC self-coding procedure, not strictly NS-SEC classes (footnote 6). Classification choices that are mine: I treated the MCA as a separate experiment because it is a distinct analysis with its own result; the web survey is classed 'partial' because it delivered granular profiles but failed as a representative instrument, and the failed-weighting finding is classed 'negative-not-achievable' with valence 'informs' because it does not decide the hypothesis; the 'only 39%' and 'no clear occupational affiliation' findings are classed 'informs' as descriptive outcomes. The paper is inductive and does not state a formal falsifiable hypothesis; the 'hyp' quote is the authors' stated contribution. No statistical uncertainty (confidence intervals, p values, class-assignment probabilities, MCA variance explained) is reported anywhere in the text; the only model-fit statistic is BIC = 12991.8. The GfK survey's representativeness is asserted ('Tests from its field division and by ourselves indicate that its demographics are nationally representative') without numbers. Footnote 10 notes the method is strictly latent profile analysis.
An experiment for each open issue
Open an issue to see the experiment proposed for it. Each design has to name a control and say what it could detect, because this registry counts a null result as evidence of absence only when a control passed and a sensitivity is stated. Where that could not be derived from what is published, the design says so rather than inventing a number.
ISS Whether 'emerging' cultural capital is a robust form of capital that competes with established forms is unresolved and said to warrant further investigation. (open-question)
The second axis of the paper's multiple correspondence analysis separates highbrow taste from what the authors call 'emerging' taste, but the paper never shows that emerging taste behaves like a capital, that is, that it converts into advantage rather than just marking out younger respondents.
- Question
- Does emerging cultural capital predict later earnings growth and promotion once highbrow cultural capital, education, occupational class, age and birth cohort are held constant?
- Hypothesis
- In a United Kingdom probability-sample panel, a one standard deviation rise in emerging cultural capital predicts higher later earnings over and above highbrow cultural capital, education and age.
- Attempt type
computational
Vocabulary note: This is secondary statistical analysis of existing social-survey microdata. The NRR value 'computational' is shaped for simulation, modelling and machine-learning work; 'evidence-synthesis' is wrong because no published effect estimates are being pooled. 'computational' is the closest of the five but describes the tooling, not the kind of inquiry.- Design
- Use a United Kingdom probability-sample household panel that carries both a cultural participation module and repeated earnings, which is the design Reeves and de Vries used to test convertibility of cultural consumption. Subjects are working-age adults observed in at least two waves. First reconstruct two cultural capital scores from the panel's cultural items using the same specific multiple correspondence analysis the paper used, and report how many of the paper's 27 cultural variables the panel actually carries. Then fit three nested specifications of a person fixed-effects earnings model and a discrete-time promotion model: highbrow score only, emerging score only, and both scores together, each with age, birth cohort, education, occupational class and region. The pre-registered primary outcome is the coefficient on the standardised emerging score in the both-scores specification. Repeat the whole estimation inside a single ten-year birth cohort. The analysis window is the earliest and latest waves that carry both the cultural module and earnings.
- Controls
known-positive-taskThe highbrow cultural capital score entered in the same models. Reeves and de Vries (2018) report that people who consume more cultural activities earn higher wages later, are more upwardly mobile and are more likely to be promoted.
Rules out: A null on the emerging score caused by a broken score reconstruction, a mis-specified earnings model or a panel whose cultural items carry no signal at all.
Vocabulary note: In NRR this value means a benchmark task with a known-good answer. Here it is a predictor with a published positive effect used the same way: if it fails to recover, the pipeline is broken rather than the hypothesis refuted.within-subjectPerson fixed effects, so each respondent is compared with themselves across waves rather than with other respondents.
Rules out: That the association is driven by stable unobserved differences between people, such as family background, personality or region of upbringing, rather than by cultural capital.designatedA replication restricted to one narrow birth cohort, so the emerging score cannot stand in for being young.
Rules out: That 'emerging cultural capital' is an age or cohort marker rather than a form of capital. Prieur, Savage and Flemmen (2023) state that in many later studies the second axis of the social space turns out to be structured by age rather than by capital composition, which is exactly this alternative.
Vocabulary note: Used here as an age placebo rather than as a designated positive control sample.
- Sensitivity
- Cannot be set from what is published. The record gives the GfK means and standard deviations for the two scores (highbrow 10.3, standard deviation 4.9; emerging 13.5, standard deviation 6.3, on maxima of 30 and 32), which is enough to standardise an effect but not to predict one: no earnings model, no variance explained and no eigenvalues are reported anywhere in the paper, and the record states explicitly that no statistical uncertainty is reported in the text. To set a minimum detectable effect this design needs (a) the per-activity earnings coefficient and its standard error from Reeves and de Vries (2018), which I did not read in numbers, and (b) the within-person variance of a reconstructed emerging score in the chosen panel, which requires a pilot run on that panel.
- Would count as
- Supported →
positive· opposed →negative-no-association
Inconclusive if: The panel's cultural items do not reproduce a two-axis solution with a recognisable highbrow versus emerging contrast. There would then be no distinct emerging dimension to test, and a null would be a statement about the panel's questionnaire rather than about emerging cultural capital. - Already done
- The concept this issue asks about was set out in its own right: Prieur and Savage argue that cultural capital is being updated and that new, 'emerging' forms coexist with the established highbrow form. (Prieur and Savage 2013, European Societies, doi:10.1080/14616696.2012.748930)
So: The theoretical half of the question is already developed, so the design should not re-argue the concept and should go straight to convertibility. - Cultural consumption does function as capital in some labour-market settings: in the United Kingdom panel Understanding Society, people who consume more cultural activities are more likely to earn higher wages later, to be upwardly mobile and to be promoted. (Reeves and de Vries 2018, British Journal of Sociology, doi:10.1111/1468-4446.12374)
So: The convertibility test has already been run for cultural consumption in general, so the only new contribution available is to split the measure into highbrow and emerging and ask which one carries the return. That becomes this design's whole point, and it supplies the positive control. - The age interpretation is already on the table: later studies repeatedly find the second axis of the social space structured by an opposition between young and old rather than between cultural and economic capital, and this had not been adequately addressed. (Prieur, Savage and Flemmen 2023, British Journal of Sociology, doi:10.1111/1468-4446.13002)
So: The age confound is the central rival explanation, which is why the within-cohort replication is a required arm and not an extra. - Emerging cultural capital has been measured and profiled since, and found to be concentrated in large urban centres: Savage, Hanquinet, Cunningham and Hjellbrekke show a close association between urban sites and residents holding new kinds of 'cosmopolitan cultural capital' in London and Brussels. (Savage, Hanquinet, Cunningham and Hjellbrekke 2018, International Journal of Urban and Regional Research, doi:10.1111/1468-2427.12531)
So: Place is a second confound with age, so region has to be in the model, and a London or metropolitan indicator should be reported separately rather than absorbed. - The underlying structure has been reproduced on richer data without imposing highbrow and lowbrow categories in advance: Flemmen, Jarness and Rosenlund recover a first dimension of volume of capital and a second of composition of capital from 168 lifestyle items in Norway, and explicitly avoid predefined notions of highbrow and lowbrow taste. (Flemmen, Jarness and Rosenlund 2017, British Journal of Sociology, doi:10.1111/1468-4446.12295)
So: It is the strongest methodological objection to this design: scoring respondents on a pre-labelled 'emerging' scale is the step they refuse. The design should report the inductive two-axis solution before scoring anyone. - The cultural markers used in the paper have already been attacked as selective: Bradley argues the markers of cultural capital skew the findings and produce a negative view of working-class culture. (Bradley 2014, Sociology, doi:10.1177/0038038514520855)
So: If the emerging score carries no earnings return, that result will be read as confirming Bradley's measurement critique rather than as evidence about capital, so item coverage has to be reported before any coefficient. - Lifestyle may be explained by education rather than by class or status at all: using three pooled waves of the Taking Part survey (n = 78,011), Reeves finds both social status and social class insignificantly associated with each of five latent arts-participation clusters, while education remains strongly correlated. (Reeves 2014, Sociology, doi:10.1177/0038038514547897)
So: Education is the rival explanation with the best existing evidence behind it, so it has to be a covariate and the design should report the emerging-score coefficient with and without it.
Searched: Searched OpenAlex for works citing the paper (OpenAlex W2141028849, 1300 citations, 269 of them published 2013 to 2016) and filtered to sociology, Poetics and Cultural Sociology outlets; searched OpenAlex by title and author for the emerging cultural capital line of work (Prieur and Savage, Savage and Hanquinet, Flemmen, Jarness, Rosenlund) and for returns to cultural capital; retrieved OpenAlex abstracts for each item cited above. I looked for but did not find a study that reconstructs the paper's two cultural capital scores on a probability sample and estimates separate economic returns to each, which is why this design is still open.
- The concept this issue asks about was set out in its own right: Prieur and Savage argue that cultural capital is being updated and that new, 'emerging' forms coexist with the established highbrow form. (Prieur and Savage 2013, European Societies, doi:10.1080/14616696.2012.748930)
- Feasibility
- A quantitative sociology or social statistics group with access to a United Kingdom household panel through the UK Data Service, or the panel's own research team. · 9 to 15 months · low, because it is secondary analysis of an existing panel and needs analyst time and data access only, no fieldwork
Blockers: The panel's cultural module may not overlap enough with the paper's 27 cultural variables to reconstruct an emerging score at all; Cultural modules are usually fielded once, so a within-person design may have only one cultural measurement and must treat it as time-invariant; Promotion is not measured directly in most panels and would have to be derived from job spells and occupation changes - Strongest objection
- A Bourdieusian specialist would say the design tests the wrong conversion. Capital is relational, and its value is realised through recognition and legitimacy as much as through wages, so an earnings null would not show that emerging cultural capital is not a capital; it would show only that this particular conversion does not pay in this labour market. The sharper version of the objection is Flemmen, Jarness and Rosenlund's: labelling items 'emerging' in advance and scoring people on that label is the substantialist fallacy, so the independent variable is an artefact of the analyst's own classification.
- Not derivable from what is published
- The item wording of the paper's 27 cultural variables, so the overlap with any panel's cultural module cannot be assessed in advance
- The eigenvalues or variance explained by the two multiple correspondence analysis axes, which the record states are not reported anywhere in the paper
- The published size and standard error of the earnings return to cultural consumption, needed to set a minimum detectable effect
- Whether the emerging score's apparent youth loading is an age effect or a cohort effect, which the paper cannot distinguish from one cross-section
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ISS Household measures of income, savings and house value obscure within-household divisions, so relationships between gender and class are not fully registered. (open-question)
Three of the six inputs to the latent class model are household quantities, which makes two partners in the same couple identical on half the economic side of the model, and the authors flag that this hides the relationship between gender and class.
- Question
- Does replacing household income, savings and house value with individually held amounts change the number of latent classes selected and the gender composition of each class?
- Hypothesis
- Re-running the same six-variable latent profile model with individual rather than household economic capital moves partnered women down the class solution and changes the selected class count.
- Attempt type
computational
Vocabulary note: This is a re-specification of a latent variable model on survey microdata. 'computational' is the closest of the five NRR values but implies simulation or machine learning rather than secondary survey analysis; none of the five has a value for re-estimating a published statistical model under an alternative measurement.- Design
- Use a United Kingdom probability survey that measures income and wealth at the individual level within couples, such as the Office for National Statistics Wealth and Assets Survey, which records individually held wealth. Build the six capital measures twice from the same respondents: a household version matching the paper, and an individual version in which income, savings and property wealth are the respondent's own. Fit latent profile models for two to twelve classes under both specifications with identical estimation settings, identical standardisation and the same Bayesian Information Criterion selection rule, and pre-register the class range and the number of random starts. Primary outcomes are the class count each specification selects, the adjusted Rand index between the two assignments among partnered respondents, the female share of each class under each specification, and the share of couples where the two partners fall in different classes. The stopping rule is the pre-specified class range; no class count is chosen after seeing the gender results.
- Controls
within-subjectPartner-to-partner comparison inside the same household, so each woman is compared with the man she lives with.
Rules out: That any gender difference in class placement comes from differences between households, such as region or tenure, rather than from the division of resources inside the household.
Vocabulary note: The unit held constant is the couple rather than the person, which the vocabulary does not distinguish.designatedThe same two-specification comparison run on single-adult households, where household and individual measures are the same quantity by construction.
Rules out: That the difference between the two solutions is an artefact of the re-coding pipeline, the standardisation or the estimator, since among single-adult households it should be close to zero.
Vocabulary note: Used as a null-case sample rather than a designated positive sample.no-treatmentThe paper's published household specification, re-estimated by this team on the new data before any individual-level variant is fitted.
Rules out: That differences between the two solutions reflect the change of dataset rather than the change of measurement.
Vocabulary note: There is no treatment to withhold. This records that the design has no intervention arm, which is why a conventional negative control cannot be specified. The honest statement is that the baseline is the paper's own published household specification.
- Sensitivity
- Partly derivable from the record, with the derivation mine rather than the paper's. The record gives the GfK class shares (6, 25, 6, 15, 14, 19 and 15 per cent) at n = 1026. At that sample size the standard error on a 6 per cent share is 0.74 percentage points and on a 15 per cent share 1.11 percentage points, so a shift in any single class share smaller than roughly 1.5 to 2.2 percentage points would sit inside sampling noise. The smallest classes hold about 62 respondents, which is why a replication needs a larger probability sample than GfK's to detect a gender-composition change within a class. The expected size of the within-couple wealth gap cannot be set from the record at all: no United Kingdom within-couple figure was obtained, and the published within-couple work I found is German and European rather than British.
- Would count as
- Supported →
positive· opposed →negative-no-effect
Inconclusive if: The chosen survey measures wealth jointly for couples and assigns it to partners by an imputation rule, as most surveys do. The comparison would then test the imputation rule rather than the within-household division, and neither a change nor a null would be interpretable. - Already done
- The gender objection was made directly against this paper: Bradley argues the approach is gradational rather than relational, that the cultural capital markers are selective, and that the latent classes are better described as class fractions. (Bradley 2014, Sociology, doi:10.1177/0038038514520855)
So: This is the published statement of the issue, so the design should be framed as answering Bradley rather than as a new observation, and it should report class fractions as an alternative reading of any changed solution. - The authors answered the critical reception without conceding the measurement point: they separate four strands of debate and argue for a concept of class not reducible to a single technical measure, defending the seven classes as pointing towards elite formation. (Savage, Devine, Cunningham and Friedman 2014, Sociology, doi:10.1177/0038038514536635)
So: The reply shifts the ground to elite formation, so a design that only re-specifies economic capital will be read as answering a question the team no longer treats as central; the elite class has to be reported separately. - The lead author later accepted the intersectionality point explicitly, listing the inherent intersectionality of class with other divides, notably race and gender, as one of three trends the survey crystallised, and arguing for centring wealth and property. (Savage 2025, Mens en Maatschappij, doi:10.5117/mem2025.2.002.sava)
So: Twelve years on this is a conceded open question rather than a contested one, which raises the bar: the design has to produce a number, not another argument that household measures are inadequate. - The gendered structure of the Bourdieusian social space has since been analysed in its own right, as a gendered correspondence between the social and the symbolic space. (Atkinson 2017, European Societies, doi:10.1080/14616696.2017.1371319)
So: Work already exists on gender inside this framework using correspondence analysis, so the distinctive contribution here has to be the latent class re-specification and the partner-to-partner comparison, not the observation that the space is gendered. - Wealth is measurably unequally distributed inside couples: Grabka, Marcus and Sierminska document within-couple wealth distribution rather than treating the household as a unit. (Grabka, Marcus and Sierminska 2013, Review of Economics of the Household, doi:10.1007/s11150-013-9229-2)
So: It establishes that the within-couple gap is large enough to be worth measuring, and supplies the measurement approach, but it is German data so it cannot set the expected United Kingdom effect size. - The gender wealth gap has been estimated comparatively across European countries, so individual-level wealth measurement in household surveys is an established practice. (Schneebaum, Rehm, Mader and Hollan 2017, Review of Income and Wealth, doi:10.1111/roiw.12281)
So: It shows the individual-level variables this design needs do exist in European survey infrastructure, which makes the data-availability blocker an empirical question about the United Kingdom rather than a reason not to try. - Within-household sharing of resources and household decision making have an established measurement literature of their own. (Himmelweit, Santos, Sevilla and Sofer 2013, Journal of Marriage and Family, doi:10.1111/jomf.12032)
So: It warns that individual ownership and individual access to resources are different quantities, so the design should report both the ownership-based variant and, where measured, a control-over-resources variant.
Searched: Searched OpenAlex for the critical responses to the paper published in Sociology and The Sociological Review and read their abstracts; searched OpenAlex for within-couple wealth distribution, gender wealth gap and within-household resource allocation, and for gender inside the Bourdieusian social space. I looked for and did not find any study that re-estimates the paper's seven-class latent profile model with individual rather than household economic capital, in the United Kingdom or elsewhere, nor a published within-couple wealth gap figure for the United Kingdom.
- The gender objection was made directly against this paper: Bradley argues the approach is gradational rather than relational, that the cultural capital markers are selective, and that the latent classes are better described as class fractions. (Bradley 2014, Sociology, doi:10.1177/0038038514520855)
- Feasibility
- A social statistics group with secure-access rights to the Office for National Statistics Wealth and Assets Survey, or a national statistical institute team. · 9 to 18 months · low to moderate, because the data exist but secure-access approval and disclosure control add months of calendar time rather than money
Blockers: A survey with individual wealth may not carry the social and cultural capital items needed for the other three of the six inputs, in which case the model cannot be re-estimated at all; Secure-access rules may prevent reporting class shares for classes with small cell counts, which is where the gender effect is most likely to show; Partner linkage requires the survey to identify couples within households, which not all do - Strongest objection
- A stratification specialist would say individual wealth is the wrong counterfactual. For life chances what matters is access to household resources, so treating a partner with no earnings and no wealth in their own name as low-capital would make the measure worse, not better: it would classify a person who lives in a wealthy household as precariat. The standard reply in class analysis is that class position can legitimately be derived from the household, and this design assumes without argument that the individual measure is the better one.
- Not derivable from what is published
- Whether the GfK and GBCS questionnaires asked about income, savings and property at household or individual level in a way that could be re-coded, since the record only reports the household quantities
- Whether either dataset identifies partners within a household, which the partner-to-partner control requires
- A United Kingdom within-couple wealth gap figure to set the expected effect size
- The estimation software, standardisation and number of random starts behind the published Bayesian Information Criterion value of 12991.8, which the replication would need to match
- The canonical citation for the derived-class-position argument, which I did not verify and so have stated without attribution
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ISS GBCS respondents in routine and semi-routine jobs are untypical of their peers, so extrapolating occupational profiles to lower social classes needs caution. (open-question)
The paper warns in a footnote that its own occupational profiles cannot be trusted at the bottom of the occupational hierarchy, and asks for caution, but it offers no way to say how large the problem is or whether anything fixes it. The authors also state that simple weighting was not possible.
- Question
- How large is the web survey bias in class profiles at each level of the occupational hierarchy, and does anchoring on a probability sample beat post-stratification?
- Hypothesis
- Bias in web-survey class profiles grows as occupational status falls, and a Bayesian probability-sample anchor cuts bias at the bottom more than post-stratification to national proportions.
- Attempt type
evaluation
Vocabulary note: In NRR 'evaluation' means scoring a model or agent against a benchmark task. Here what is scored is three survey estimators against a probability-sample benchmark, which is the same shape of activity on a different kind of object. 'computational' was the runner-up and describes the tooling, but 'evaluation' describes what the experiment is for.- Design
- Compare three estimators of the same target quantities: the distribution of latent classes within each self-coded occupational category, and the class profile of named occupations. Estimator one is the unweighted web survey. Estimator two is the web survey post-stratified to national occupational proportions, the correction the paper reports as not possible. Estimator three is a Bayesian combination in which the probability sample supplies the likelihood and the web survey supplies informative priors, following the approach Wisniowski and colleagues and Sakshaug and colleagues set out for supplementing small probability samples with non-probability data. The benchmark is a United Kingdom probability survey carrying the same or mapped occupational and capital items. For each estimator report absolute bias and root mean squared error per occupational category, credible or confidence interval coverage, and bias plotted against the category's mean occupational status so the monotonicity claim is directly testable. Reproduce the record's observed-to-national ratios as an anchor.
- Controls
designatedThe professional and managerial categories, where the record states that footnote 11 claims comparisons between professional and managerial occupations and between universities are robust.
Rules out: That measured bias is an artefact of mapping items between the web survey and the benchmark. If large bias appears where the authors themselves claim robustness, the mapping is wrong rather than the web survey biased.backgroundSplit-half use of the probability sample: one half is treated as the benchmark and the other as the comparison, so benchmark sampling error is estimated on its own.
Rules out: That apparent bias is benchmark noise. With a benchmark of only about a thousand cases this is the dominant alternative explanation, not a minor one.adversarial-labelA permutation run in which web-survey respondents are assigned occupational categories at random.
Rules out: That the bias metric is insensitive. Under permutation the metric must rise to the no-information level; if it does not, the metric cannot detect bias and no null from this design means anything.
Vocabulary note: In NRR this means a deliberately wrong label in a machine-learning sense. Here it is a pre-registered permutation null: occupational categories are shuffled across web-survey respondents.
- Sensitivity
- Partly derivable from the record, with the arithmetic mine. Table 1 in the record puts the bias to be corrected at about 11 percentage points for routine workers (3.2 per cent in the web sample against 14.5 per cent nationally, ratio 0.22), about 10 points for semi-routine workers (4.9 against 15.3) and about 13 points in the other direction for traditional professionals (17.9 against 4.8, ratio 3.73). The benchmark is n = 1026, so the standard error on a 14.5 per cent proportion is 1.10 percentage points and a two-sided 95 per cent interval is about 2.15 percentage points wide either side. A correction that leaves more than roughly 2.2 percentage points of residual bias at the bottom of the hierarchy is therefore detectable against that benchmark, and differences smaller than that need a larger benchmark sample.
- Would count as
- Supported →
positive· opposed →negative-not-achievable
Inconclusive if: The deposited web-survey microdata do not carry the auxiliary variables needed to match the benchmark survey, for example no region, household composition or education detail. Neither post-stratification nor the Bayesian anchor could then be fitted, and the exercise would measure data availability rather than estimator performance. - Already done
- The critique is already published and sharp: Mills argues the web survey plays no serious role in generating the typology, calls the analysis a theory-free data-dredging exercise, and says the typology is arbitrary and determined by a contingent fact, the size of the sample. (Mills 2014, Sociology, doi:10.1177/0038038513519880)
So: It settles that the selection problem is a live objection and adds a second one this design must respect: the class count itself depends on sample size, so any estimator comparison has to hold the class solution fixed rather than re-selecting it. - Mills returned to it and stated the specific unresolved point: at the heart of the team's later elite papers is an unavoidable incoherence arising from response bias which, despite protestations to the contrary, has not been dealt with properly, leaving the empirical analysis without much value. (Mills 2015, The Sociological Review, doi:10.1111/1467-954x.12287)
So: As of 2015 the published position is that the bias was never corrected, so this design is still open; it also means the result will be read as adjudicating between Mills and the team, which raises the standard of pre-registration. - The team's own account of what they did: Devine and Snee describe the construction and launch of the web survey, the response rate, why a face-to-face nationally representative survey was commissioned to deal with sample skew, and how the skew was recast as rich granular data on the most privileged. (Devine and Snee 2015, The Sociological Review, doi:10.1111/1467-954x.12282)
So: It is the primary source for what correction was actually attempted, so it defines the baseline this design has to beat, and it should be read before the estimators are specified. - Selection bias in web surveys is a characterised problem with a standard framework and standard correction families. (Bethlehem 2010, International Statistical Review, doi:10.1111/j.1751-5823.2010.00112.x)
So: It supplies the vocabulary and the standard corrections, so the design should not invent a method and should report where its estimators sit in that taxonomy. - Correcting a non-probability sample requires strong and checkable assumptions: Mercer, Kreuter, Keeter and Stuart set out the conditions under which non-probability samples can support inference, and Elliott and Valliant review the available inferential frameworks. (Mercer, Kreuter, Keeter and Stuart 2016, Public Opinion Quarterly; Elliott and Valliant 2017, Statistical Science, doi:10.1093/poq/nfw060)
So: These set the assumptions this design must state explicitly, in particular that the auxiliary variables available have to explain both participation and the outcome; if they do not, no estimator can work and the honest result is the inconclusive one. - The specific fix this design proposes has been developed and tested: Wisniowski, Sakshaug, Perez Ruiz and Blom combine probability and non-probability samples in a Bayesian framework and show that informative priors from non-probability data reduce variance and mean squared error for linear model coefficients, and Sakshaug and colleagues set out supplementing small probability samples with non-probability samples. (Wisniowski, Sakshaug, Perez Ruiz and Blom 2019, Journal of Survey Statistics and Methodology; Sakshaug, Wisniowski, Perez Ruiz and Blom 2019, Journal of Official Statistics, doi:10.1093/jssam/smz051)
So: The method already exists and is validated for linear model coefficients, so the contribution here is applying it to a latent class distribution, and the design should say plainly that the published validation does not cover latent class models. - Model-based correction of a badly skewed opt-in sample can recover population quantities: Wang, Rothschild, Goel and Gelman forecast elections from non-representative polls using multilevel regression and post-stratification. (Wang, Rothschild, Goel and Gelman 2014, International Journal of Forecasting, doi:10.1016/j.ijforecast.2014.06.001)
So: It is the existence proof that the paper's claim that weighting was not possible is a claim about the available auxiliary variables, not a general result, and it suggests a fourth estimator worth adding. - Probability samples outperform non-probability internet samples on accuracy against population benchmarks. (Yeager, Krosnick, Chang, Javitz and colleagues 2011, Public Opinion Quarterly, doi:10.1093/poq/nfr020)
So: It sets the prior expectation that the unweighted web survey will lose, which means the informative comparison is between the two corrected estimators, not between the web survey and the benchmark.
Searched: Searched OpenAlex for works citing the paper in sociology outlets 2013 to 2016 and read the abstracts of both Mills pieces, the authors' reply and the team's own methodological paper; searched OpenAlex for web-survey selection bias, non-probability inference, probability and non-probability sample integration, and multilevel regression and post-stratification, verifying each DOI. I searched specifically for a published quantification of the web survey's bias by occupational level and for a critique by Griffiths and Lambert, and found neither; the only published statements remain qualitative, that the bias was not properly dealt with.
- The critique is already published and sharp: Mills argues the web survey plays no serious role in generating the typology, calls the analysis a theory-free data-dredging exercise, and says the typology is arbitrary and determined by a contingent fact, the size of the sample. (Mills 2014, Sociology, doi:10.1177/0038038513519880)
- Feasibility
- A survey methodology group with access to the deposited web-survey and probability-sample microdata, working with a national probability survey holder. · 12 to 18 months · moderate, because the estimators are cheap but matching items across two surveys and obtaining the benchmark microdata is the bulk of the work
Blockers: The deposited microdata may not carry occupational codes at the detail the paper's Table 8 uses; No benchmark survey is likely to carry the paper's social and cultural capital items, so the class solution may have to be imputed into the benchmark rather than estimated in it; The web survey has no response rate denominator in the record, so participation propensities cannot be modelled directly; Mode differences between a self-completed web instrument and a face-to-face interview will be confounded with selection - Strongest objection
- A survey statistician would object that there is no well-defined quantity to correct towards. The web survey had no sampling frame and no measurable response propensities, so any bias estimated is bias relative to a benchmark whose items were collected in a different mode by a different firm, and the exercise would largely measure mode and wording differences. Mills's version is blunter: the bias is in who chose to turn up, nothing in the data identifies that, and dressing the problem in Bayesian machinery does not create the missing information.
- Not derivable from what is published
- Whether the web-survey microdata are deposited at all, and if so with what occupational coding detail
- The response rate: the record gives 161,400 completes by July 2011 with no denominator, so participation cannot be modelled
- Whether any probability survey carries the social and cultural capital items needed to estimate the class solution in the benchmark
- The exact definition of the self-coded occupational categories in Table 1, which the record notes are from the National Statistics Socio-economic Classification self-coding procedure and are not strictly its classes
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ISS Fuller accounts of educational and occupational profiles (including specific universities) and cross-fertilisation with qualitative research are deferred to future work. (next-step)
This is the authors' own deferred plan, and they largely carried it out: the 2015 special issue of The Sociological Review delivered the universities and the elite occupations. What they left unspecified is the control and the comparator. The university profiles were computed on the skewed web sample with no probability or administrative benchmark, and the qualitative cross-fertilisation happened as separate studies rather than as a design in which one can correct the other.
- Question
- Do the web survey university-by-class profiles survive a benchmark that does not share its selection, and does a blinded qualitative assignment agree with survey-based class?
- Hypothesis
- The reported ranking of universities by graduate economic capital holds against an administrative benchmark, but absolute levels are inflated and the gradient compressed where coverage is thinnest.
- Attempt type
computational
Vocabulary note: A poor fit, and worth recording. Arm A is secondary data linkage and benchmarking, for which 'computational' is the closest value. Arm B is primary qualitative fieldwork plus blinded human coding, for which the vocabulary has no value at all: the only primary-data-collection value is 'wet-lab', which is plainly wrong, and 'evidence-synthesis' does not cover collecting new data. A mixed-methods design cannot be labelled correctly with one value from this list.- Design
- Arm A, quantitative benchmark. Take the web survey's graduate subsample, which Wakeling and Savage report as over 85,000 graduates, and compare the institution-level distribution of graduates and their economic capital against an administrative or probability benchmark covering the same institutions and graduation cohorts. Outcomes are the Spearman rank correlation between the two institution rankings, and the mean signed difference in each institution's graduate income percentile. Institutions below a pre-specified web-survey cell count are reported separately and excluded from the primary correlation. Arm B, nested qualitative. Draw a stratified sub-sample from the benchmark frame rather than from the web survey, interview each person about trajectory, education and taste, and have two coders independently assign each to one of the seven classes while blind to the survey-based assignment. The outcome is Cohen's kappa between coder assignment and survey assignment. Total duration about 18 months.
- Controls
designatedThe Oxford, Cambridge and London institutions that Wakeling and Savage identify as a distinct elite, where web-survey cell counts are largest and the reported gradients sharpest.
Rules out: That a failure to reproduce the ranking is a linkage or scaling failure rather than a selection effect, since this is the part of the ranking that should reproduce if the pipeline works.backgroundInstitutions with small web-survey cell counts, analysed and reported separately from the primary comparison.
Rules out: That compression of the gradient at lower-ranked institutions is caused by selection, when it could be caused by small cell counts and the resulting regression towards the mean.adversarial-labelFor arm B, a set of decoy cases in which coders are shown a shuffled survey profile alongside the interview.
Rules out: That the agreement statistic is driven by coders inferring the survey-based class or the hypothesis rather than by the interview material.
Vocabulary note: A blinding check rather than a corrupted training label.
- Sensitivity
- Not derivable from the record, and this is the honest answer. The paper reports no university-level or institution-level numbers at all; the figure of over 85,000 graduates comes from Wakeling and Savage 2015, not from the paper being designed for. To set a minimum detectable difference in rank correlation this design needs the number of institutions covered and the per-institution web-survey cell counts, neither of which is published. For arm B a kappa study needs a target value and a pilot agreement rate, and no qualitative class-assignment reliability study was found to supply either. What would settle it: a published table of web-survey graduate counts by institution, and a pilot in which two coders assign thirty interviews to the seven classes so an observed agreement rate exists.
- Would count as
- Supported →
positive· opposed →negative-not-reproducible
Inconclusive if: The administrative benchmark reports graduate earnings by institution only in bands coarser than the web survey's economic capital measure. The two could not be put on a common scale, the signed-difference outcome would be unavailable, and only the rank comparison would survive. - Already done
- The universities half of this next step was done: Wakeling and Savage used the web survey to examine over 85,000 graduates, found distinct stratification of outcomes by university attended even within the Russell Group, and identified a golden triangle of Oxford, Cambridge and certain London institutions as a distinct elite, with Oxford ahead of Cambridge on several measures. (Wakeling and Savage 2015, The Sociological Review, doi:10.1111/1467-954x.12284)
So: This is the authors' own delivery of the ISS, so the design must be framed as supplying the benchmark they lacked rather than as a new idea, and their reported ranking is the hypothesis to be tested. - The occupational half was also done: Friedman, Laurison and Miles analysed social mobility into Britain's elite occupations from the same survey. (Friedman, Laurison and Miles 2015, The Sociological Review, doi:10.1111/1467-954x.12283)
So: It removes the occupational profiling part of this ISS from the design's scope and leaves only the benchmarking question. - The same team went on to find a class pay gap within higher professional and managerial occupations, moving the question from entry to rewards. (Laurison and Friedman 2016, American Sociological Review, doi:10.1177/0003122416653602)
So: It shows the field has moved to earnings differences within occupations, so a design that only reproduces an institution ranking is answering a superseded question unless it also reports within-institution spread. - Elite recruitment by school has since been measured against an independent historical source rather than a self-selected survey: Reeves, Friedman, Rahal and Flemmen trace private schooling among British elites from 1897 to 2016. (Reeves, Friedman, Rahal and Flemmen 2017, American Sociological Review, doi:10.1177/0003122417735742)
So: It is the methodological template this design should follow: an external frame rather than a self-selected one, which is precisely the control the web-survey university papers lack. - The geographical half of the elite profiling was also published from the same survey. (Cunningham and Savage 2015, The Sociological Review, doi:10.1111/1467-954x.12285)
So: It means the benchmark comparison should include region, because the reported elite is geographically concentrated and any benchmark with different regional coverage will differ for that reason alone. - The qualitative cross-fertilisation has effectively been attempted as a comparison rather than as a joint design: Silva situates the survey against the Cultural Capital and Social Exclusion project, which ran from 2003 to 2006, and raises the implications of the turn to big data for the project's procedures and claims. (Silva 2015, The Sociological Review, doi:10.1111/1467-954x.12286)
So: This is the nearest existing answer to the qualitative half of the ISS, and it is critical rather than integrative, which is the gap arm B is designed to fill with a nested sample and blinded coding. - The team published their own account of the project's history, the handling of sample skew and their future plans, introducing the special issue that delivered most of this ISS. (Devine and Snee 2015, The Sociological Review, doi:10.1111/1467-954x.12282)
So: It is the authoritative statement of what the authors intended by this deferred next step, so it defines what counts as completing it. - The elite papers that delivered this ISS were themselves judged unsound: Mills argues the elite is not well defined by the procedures used to identify it and that the response bias was never properly handled. (Mills 2015, The Sociological Review, doi:10.1111/1467-954x.12287)
So: It is the reason the benchmark arm is the whole point: without an external comparator the university findings cannot be defended against this objection.
Searched: Searched OpenAlex for works citing the paper and filtered to The Sociological Review's 2015 special issue, then used Crossref to enumerate and verify the adjacent articles in that issue, which surfaced Devine and Snee, Silva, Mills and the elite papers; verified each DOI and read the OpenAlex abstracts for Wakeling and Savage, Silva, Devine and Snee. I looked for and did not find any study benchmarking the web survey's university-level profiles against an administrative or probability source, and did not find a qualitative study that assigns interviewees to the seven classes blind to their survey assignment.
- The universities half of this next step was done: Wakeling and Savage used the web survey to examine over 85,000 graduates, found distinct stratification of outcomes by university attended even within the Russell Group, and identified a golden triangle of Oxford, Cambridge and certain London institutions as a distinct elite, with Oxford ahead of Cambridge on several measures. (Wakeling and Savage 2015, The Sociological Review, doi:10.1111/1467-954x.12284)
- Feasibility
- A higher education research group with access to a graduate outcomes administrative dataset, paired with a qualitative sociology team. · 18 to 24 months · high, because arm B is primary fieldwork with two independent coders and arm A needs secure administrative data access
Blockers: Recontacting web-survey respondents for arm B requires consent terms that the record does not state, which is why arm B samples from the benchmark frame instead; Administrative graduate earnings are individual and tax-based while the web survey's economic capital is self-reported and partly household, so a systematic difference is expected by construction; Institution name may not have been captured in a codeable form in the web survey; Cohort coverage of any administrative benchmark may not reach the older graduates in the web survey - Strongest objection
- Most of this ISS has already been delivered, so a specialist would say the design is a decade late and the residual question is narrow. The sharper objection is that the benchmark comparison is confounded by construction: administrative earnings are individual and tax-recorded, the web survey's economic capital is self-reported and includes household income, savings and house value, so a systematic gap between them is guaranteed and says nothing about selection. Arm B invites a second objection, that assigning interviewees to seven latent classes by hand treats a statistical artefact as a social category that people can be recognised as belonging to.
- Not derivable from what is published
- Web-survey graduate counts by institution, needed to set the cell-count threshold and the sensitivity
- Whether the web survey captured institution name in a codeable form
- Whether the deposited data permit linkage to any administrative source, and under what consent terms
- Whether any qualitative interviews were conducted alongside the survey and are archived, which would change arm B from new fieldwork to secondary analysis
- A pilot inter-coder agreement rate for assigning people to the seven classes from interview material
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Designed on 20 October 2026 against outreach/sage-experiments/brief.md. Grounded on: record, prior-art. Full text: not obtained: Europe PMC returned hitCount 0 for DOI:"10.1177/0038038513481128" (sociology is not indexed there), and the brief forbids spending turns on journals.sagepub.com, which refuses plain HTTP requests. Every number below that is attributed to this paper comes from the graph JSON record, not from the article text.. Designer notes: FULL TEXT. Not obtained. Europe PMC returned hitCount 0 for the DOI, as expected for a sociology title, and the brief rules out journals.sagepub.com. Everything attributed to the paper comes from the graph JSON record. Where I used a number the record does not contain, I have named its source in prior art. FOUR DESIGNS, one per ISS node, in record order. WHAT THE PUBLISHED CRITIQUES ALREADY SETTLE. This paper drew a named critical literature within a year, and it closes off several designs. Mills 2014 (doi:10.1177/0038038513519880) argues the web survey plays no serious role in generating the typology, calls the method a theory-free data-dredging exercise, and argues the seven classes are an arbitrary typology determined by the size of the sample. That last point is the one with teeth for iss-3: because the Bayesian Information Criterion penalty scales with sample size, a defence of the seven-class count cannot be mounted on the published record, and the record itself notes that BIC = 12991.8 is the only fit statistic reported anywhere. Mills 2015 (doi:10.1111/1467-954x.12287) states that the response bias was never properly dealt with and that the resulting analysis is without much value, which means iss-3 was still open as of 2015 and no later quantification was found. Bradley 2014 (doi:10.1177/0038038514520855) makes the iss-2 argument in print: the approach is gradational rather than relational, the cultural markers are selective, and the latent classes are better read as class fractions. Savage et al. replied in 2014 (doi:10.1177/0038038514536635) by separating four strands of debate and moving the defence onto elite formation, and Savage 2025 (doi:10.5117/mem2025.2.002.sava) concedes the intersectionality of class with gender and race. So iss-2 is a conceded open question rather than a contested one, which raises the bar: a design has to produce a number. iss-4 is largely already delivered by the authors themselves in the 2015 special issue of The Sociological Review: Wakeling and Savage did the universities, Friedman, Laurison and Miles the elite occupations, Cunningham and Savage the geography, and Silva (doi:10.1111/1467-954x.12286) supplied the nearest thing to the qualitative cross-fertilisation, as a critical comparison with the Cultural Capital and Social Exclusion project rather than a joint design. What is still missing there is the external benchmark, which is what the design supplies. For iss-1 the concept has been developed (Prieur and Savage 2013) and profiled (Savage et al. 2018), the convertibility test has been run for cultural consumption in general (Reeves and de Vries 2018), and the age confound has been named explicitly (Prieur, Savage and Flemmen 2023), so the only untried residual is splitting the measure and asking which half carries the return. VOCABULARY MISFIT, which the brief asks me to report. attemptType fits badly throughout. None of the five values describes secondary analysis of social survey microdata, which is what three of the four designs are; I used 'computational' for those and said so in each attemptTypeNote, but it names the tooling rather than the kind of inquiry. For iss-3 I chose 'evaluation' because the design scores estimators against a benchmark, which is structurally the same activity as scoring a model against a benchmark task, but the NRR value is written for models and agents. iss-4 is the worst fit: it is a mixed-methods design whose second arm is primary qualitative fieldwork with blinded human coding, and the vocabulary's only primary-data-collection value is 'wet-lab'. A single value cannot label it correctly. The source record shows the same strain from the other direction: its own attemptType fields are free text ('web survey (self-selected)', 'latent class analysis', 'multiple correspondence analysis'), none of which is in the controlled list. CONTROL KINDS fit worse. The negative control kinds are pharmacological and immunological (vehicle, isotype, no-treatment) and there is no treatment anywhere in a survey design, so I used 'no-treatment' once, in iss-2, purely to record that there is no intervention arm, and said so in the kindNote. What survey work actually needs are values this list does not have: a permutation or placebo null, a benchmark-noise estimate, a blinding check, and a specification baseline. I mapped those onto 'adversarial-label', 'background', 'adversarial-label' again and 'no-treatment' respectively, each with a kindNote, which is the closest available and is in every case a stretch. 'known-positive-task' I used in iss-1 for a predictor with a published effect, which is the same logical role as a positive control but not the same object. 'designated' was the most portable value: it carried an age placebo, a null-case subsample and a must-reproduce subgroup across three designs, which suggests the vocabulary would benefit from splitting it. OUTCOME CLASSES fit well. 'negative-no-association', 'negative-no-effect', 'negative-not-achievable' and 'negative-not-reproducible' each had a natural home, and 'negative-not-achievable' for iss-3 matches the class the record itself assigned to the failed-weighting finding. INFERENCES AND THIN SPOTS. The sensitivity statements for iss-2 and iss-3 use standard errors I computed from the record's own GfK percentages and n = 1026; that arithmetic is mine, not the paper's, and the paper reports no uncertainty of any kind. The iss-1 and iss-4 sensitivity statements could not be derived at all and say so, which the brief treats as a legitimate output: iss-1 needs a published earnings coefficient and a pilot variance, iss-4 needs per-institution cell counts and a pilot inter-coder agreement rate. For iss-2 I state the derived-class-position counter-argument in whyThisMightBeWrong without a citation because I could not verify the canonical reference, and I have listed that in notDerivable rather than attributing it from memory. No United Kingdom within-couple wealth gap figure was found; the within-couple work I verified is German (Grabka, Marcus and Sierminska 2013) and European (Schneebaum et al. 2017). I searched for a critique by Griffiths and Lambert, which a blog commentary refers to, and did not find an indexed article, so it is not cited. OpenAlex rate-limited me partway through, so the title-level sweep for all works with 'Great British Class Survey' in the title was not completed; the special issue was instead enumerated through Crossref, and three of the four priorArtSearch statements name what I looked for and did not find.
The other seven
- Psilocybin for depression and anxiety in cancer
- Teriflunomide versus interferon beta-1a (TENERE)
- Camouflaging in autistic men and women
- Microglia depletion after brain ischaemia
- Tyre and rider effects on bicycle stability
- Fatigue rate in the heterogeneous region of a welded joint
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Licence: this paper is CC BY on journals.sagepub.com, so the graph of it is published here with attribution, exactly as the pilot’s records are. Method: full text from SAGE full-text HTML; one extraction pass against outreach/sage-graphs/brief.md, every finding with a locator and a verbatim quote; the extraction notes above say what was inferred.