Are tattoos associated with employment and wage discrimination? Analyzing the relationships between body art and labor market outcomes

Abstract

Do job applicants and employees with tattoos suffer a penalty in the labor market because of their body art? Previous research has found that tattooed people are widely perceived by hiring managers to be less employable than people without tattoos. This is especially the case for those who have visible tattoos (particularly offensive ones) that are difficult to conceal. Given this backdrop, our research surprisingly found no empirical evidence of employment, wage or earnings discrimination against people with various types of tattoos. In our sample, and considering a variety of alternative estimation techniques, not only are the wages and annual earnings of tattooed employees in the United States statistically indistinguishable from the wages and annual earnings of employees without tattoos, but tattooed individuals are also just as likely, and in some instances even more likely, to gain employment. These results suggest that, contrary to popular opinion as well as research findings with hiring managers and customers, having a tattoo does not appear to be associated with disadvantage or discrimination in the labor market.

Keywords

discrimination Equalities labor supply tattoos wage differentials wages

Introduction

The literature on employment discrimination has traditionally focused on the myriad of disadvantages faced by job applicants and employees with legally protected characteristics, such as racial and ethnic minorities (Deitch et al., 2003; Laer and Janssens, 2011), women (Arulampalam et al., 2007; Blau and Kahn, 2006), people with disabilities (Fevre et al., 2013; Hoque et al., 2018), members of the lesbian, gay, bisexual, transgender, intersex (LGBTI) community (Bell et al., 2011; Ragins and Cornwell, 2001), the elderly (Finkelstein et al., 1995; Kunze et al., 2011), or some intersection (McBride et al., 2015) of these traits (Acker, 2006; Darity and Mason, 1998). Alongside these traditional drivers of discrimination has emerged a parallel body of research investigating labor market biases that are more difficult, if not impossible, to regulate legally. These include employer prejudices on the basis of, for example, body weight (Levay, 2014; Nickson et al., 2016), clothing and apparel (Ghumman and Ryan, 2013; King and Ahmad, 2010), and overall attractiveness (Dipboye, 2005; Hamermesh and Biddle, 1994; Robins et al., 2011). Warhurst et al. (2009) have labeled such employment discrimination ‘lookism,’ and they point out that institutional responses to it are fraught with difficulties.

One form of lookism that has received increasing scholarly attention in recent years is labor market discrimination against tattooed job seekers and employees. A small, but emerging, body of research has shown that, with a few exceptions (Timming, 2017), employers hold largely negative attitudes towards body art (Bekhor et al., 1995; Brallier et al., 2011; Swanger, 2006; Timming et al., 2017). Some ethnographic evidence also exists indicating that visibly tattooed job seekers report facing significant barriers to employment (Timming, 2015). However, the prevailing view that body art is associated with both employment and earnings discrimination was challenged by a recent study finding that having a tattoo is not significantly related to employment conditional on labor force participation, nor with earnings conditional on employment (French et al., 2016). Using a variety of econometric techniques, French and colleagues analyzed data from two large-scale, nationally representative datasets—one from the United States and the other from Australia. Their surprising results held up to a number of sensitivity analyses and robustness checks.

Despite the methodological rigor of their methods, French and colleagues acknowledge a number of limitations with their study, chief among them that the tattoo measure was a simple binary variable (whether or not the respondent has a tattoo). Thus, for the present study, we designed and administered a survey instrument and collected detailed information from a large sample of US adults (N = 2,008) on: tattoo prevalence and characteristics; several measures of labor force participation, labor supply and earnings; socio-demographics; risky behaviors; health status; and other important predictors. Even with these more extensive measures and models, we still find no evidence that tattoos are significantly associated with employment or earnings discrimination.

These results, in light of French et al. (2016) and another recent study on this topic (Dillingh et al., 2016), not only make an important contribution to the niche literature on the effects of body art in the workplace (Arndt and Glassman, 2012; Arndt et al., 2016; Bekhor et al., 1995; Brallier et al., 2011; Dean, 2010; Karl et al., 2016; Miller et al., 2009; Swanger, 2006; Timming, 2015, 2017; Timming et al., 2017), but also have important implications for the wider equalities literature. Specifically, a consensus seems to be emerging that, contrary to popular belief, tattoos do not appear to diminish one’s labor market prospects. The fact that we, along with French et al. (2016) and Dillingh et al. (2016), found no evidence of employment or earnings discrimination against tattooed people suggests that they are perhaps not, as previously expected, a marginalized, disadvantaged and oppressed group. If so, one could argue that equality and diversity researchers should continue to focus instead on groups that have experienced blatant and proven discrimination (Greene, 2015).

In the next section, we critically review the relevant literature to which our study seeks to contribute. After that, we describe the methods by which the data were collected and analyzed. The results of the research are then reported, followed by a discussion documenting the contributions to the literature and proposing some directions for future research.

Literature review

At first glance, tattooed people, as a loosely constituted social group, appear ostensibly to qualify as a disadvantaged community of individuals. Historically, tattoos have been associated with counter-cultural delinquents of the lower class (Burgess and Clark, 2010; DeMello, 1995). It has only been in the past few decades that tattooing as a form of self-expression has extended beyond its historical base of sailors, prisoners and gang members (Schildkrout, 2004). Although societal attitudes towards body art are rapidly changing (Timming, 2015), tattoos have been associated with a number of externalized risk behaviors (Deschesnes et al., 2006; Heywood et al., 2012). Based on findings from multiple studies, tattooed individuals spend more time in jail, consume more alcohol, are more likely to have tried recreational drugs, have greater problems in school, suffer from a higher rate of mental illness, and display more violent tendencies than their non-tattooed counterparts (Heywood et al., 2012; Manuel and Retzlaff, 2002; Roberts and Ryan, 2002).

This brand of tattoo stereotyping, it could be argued, runs to some extent parallel to the negative experiences of those who belong to other marginalized groups, many of whom are similarly stereotyped (Peffley et al., 1997). The presence of a tattoo signals to others that one is socially tainted or stigmatized (Goffman, 1963), a view that has been evidenced even in children as young as six years old (Durkin and Houghton, 2000). Among adults, it has been reported that people with tattoos are perceived as significantly less: athletic, attractive, motivated, honest, generous, religious and intelligent (Degelman and Price, 2002) vis-a-vis people without tattoos.

Based on these wider societal perceptions, it follows that tattooed job applicants and employees might face discrimination in the workplace, and a body of literature has emerged demonstrating this much. Bekhor et al. (1995) were the first to explore this question. They found that managers were particularly averse to the employment of visibly tattooed people in the hospitality, beauty, retail and services sector. Swanger (2006) similarly reports that upwards of 80% of human resource managers and recruiters surveyed in her study expressed negative feelings toward the visible display of tattoos on employees or prospective employees. Miller et al. (2009) found that employees prefer not to work on a team with tattooed co-workers when rewards are shared. Another study, this time conducted in the restaurant industry, found that managers preferred hiring men and women without tattoos, versus tattooed individuals, even with the same resumes (Brallier et al., 2011). More recently, Timming (2015) interviewed hiring managers in the services sector as well as visibly tattooed job seekers, and found that the genre of the tattoo, its location on the body, and whether a position is customer-facing all played a significant role in explaining employer prejudice against body art. In an extension of that study, Timming et al. (2017) found that photos of tattooed applicants were rated significantly lower on hireability scales in jobs involving customer interaction compared with photos of applicants without tattoos. In short, the cumulative evidence clearly suggests that human resource managers and recruiters have, in recent years, held widely antagonistic views toward body art.

To help understand why so many employers hold largely negative attitudes toward tattoos in the workplace, one only needs to look at the marketing literature inasmuch as most managerial decision-making is ultimately driven by the consumer. A handful of studies has examined body art in the context of relationship marketing. Dean (2010) found that older consumers view visibly tattooed workers as less intelligent and less honest than non-tattooed personnel. He also found that consumers perceived visible tattoos in white collar professions to be inappropriate, although more acceptable in blue-collar jobs. Arndt and Glassman (2012) found that customers were particularly antagonistic toward women with more masculine tattoos. Doleac and Stein (2013) found that consumers exhibited a reduced propensity to purchase when the seller of a product has a tattoo. Larsen et al. (2014) point to the continuing stigma attached to body art from the point of view of the consumer. Arndt et al. (2016) argue that context is key to customers’ perceptions of body art, and in most workplace contexts they found a negative or neutral attitude on the part of the consumer. In another relevant study, respondents in Mexico and Turkey indicated that visible tattoos would have a negative impact on customer perceptions of service quality (Karl et al., 2016). More recently, in a mixed-methods study, Timming (2017) found that tattoos can be an asset or a liability, depending on the ‘brand personality’ (Aaker, 1997) that an organization is trying to project or foster.

In aggregate, much of the existing literature, spanning human resource management and marketing, points to a significant amount of perceived discrimination against individuals with tattoos, both on the part of employers and customers. However, perceived discrimination is not the same as actual discrimination (Frieze et al., 1990), and we argue that this distinction is more than just splitting hairs. Namely, the literature reviewed thus far reports on abstract negative attitudes toward body art (e.g. whether a manager would hire a tattooed job applicant or whether a consumer would purchase a product or service from a tattooed employee), but no concrete evidence was presented on actual employment discrimination against tattooed people until two recent studies by French et al. (2016) and Dillingh et al. (2016).

French et al. (2016) sought to examine the net effect of tattoos on employment and earnings. The authors expected to find a negative relationship between the presence of body art and labor market outcomes; indeed, in bivariate analyses, tattoos were associated with lower earnings and reduced employability. But after controlling for human capital, occupational and behavioral choices, and lifestyle factors, the relationships became non-significant. Thus, the expectation that tattooed people face ‘taste-based discrimination’ in the labor market (Becker, 1971; Guryan and Charles, 2013) was simply not borne out in the data. In a similar vein, Dillingh et al. (2016), drawing from a Dutch dataset, also looked at the effect of having a tattoo on both employment and earnings. Although they found that tattoos among individuals in the Netherlands were significantly related to unemployment—corroborating the extant literature on perceived discrimination—like French et al. (2016), they also found zero net effect of body art on personal income. In short, both studies point to at least a partial disconnect between perceived and actual labor market discrimination on the basis of tattoos.

Given that the extant literature offers up a mixed and somewhat contradictory set of results regarding the effects of tattoos on individual labor market outcomes, further research is warranted to clarify these relationships—hence, the present study. At their own admission, French et al. (2016) highlight several limitations to their study, among them: (i) the key explanatory variable is potentially endogenous because obtaining a tattoo is a behavioral choice that may be significantly correlated with omitted variables that also predict employment and earnings; (ii) the tattoo measure is a simple binary variable (whether or not the respondent has a tattoo), and so is unable to account for the number of tattoos, whether or not they are visible, and the type of image (e.g. offensive vs innocuous); (iii) the labor market outcomes they used are few and imperfect (e.g. family income instead of personal income was used in the Australian dataset); and (iv) the data collection for the US survey was completed in 2008–2009 and for the Australian survey back in 2001–2002, thus rendering the analyses potentially anachronistic. The present study directly addresses each one of these limitations by: using multiple measures of tattoos, including whether the respondent has at least one tattoo, the number of tattoos, whether one or more tattoos is visible, and whether one or more tattoos is offensive; using a broader range of labor market outcomes, including employment, labor supply and earnings; estimating separate models for men and women to explore potential gender effects; and controlling for a number of human capital measures and personal characteristics that might otherwise confound the results.

Data and methods

Survey design and administration

The starting point for the design of the survey instrument was to ensure that it improved upon the above-mentioned limitations associated with French et al.’s (2016) study design. We recognized the need to collect multiple measures of respondents’ tattoos and labor market outcomes, as well as a wider range of control variables to redress potential endogeneity and omitted variables bias. We also had to decide upon a sampling method, and elected to employ Mechanical Turk (MTurk), a popular crowdsourcing platform often used by social scientists to procure large-scale samples. A general overview of the functionality of the MTurk platform can be found in Barger et al. (2011). In short, MTurk is an online space where ‘requesters’ (i.e. primarily businesses and academics) can post human intelligence tasks (HITs) for ‘workers’ (i.e. respondents) in exchange for compensation. Among academics, this platform is often used in conjunction with a survey design tool (in our case, Qualtrics) to administer the instrument. Psychologists have pioneered the use of MTurk (Paolacci and Chandler, 2014), but the platform is increasingly used across the social and political sciences (see Sheehan and Pittman, 2016) for purposes of experimental and quantitative data collection.

A total of 2064 respondents initially completed the questionnaire. All 50 states are represented in the sample, and roughly half of respondents come from urban areas with a population of over 1 million. Four items were randomly placed in the survey to provide an instructional manipulation check (Oppenheimer et al., 2009). These screening items were designed to ensure that participants were paying close attention and providing accurate responses. The first item is a simple math problem (‘What is 8 + 3?’); the second item asks respondents to select ‘5’ from a list of numbers; the third item lists 10 hobbies and asks respondents to select the two that begin with the letter ‘r’ (reading and rugby); the last item is another simple math problem (‘What is 2 + 2?’). Five respondents who provided incorrect responses to more than one of these four manipulation checks were deleted. Another 51 cases were subsequently removed owing to missing data. Thus, the final sample size is N = 2,008 cases (685 males and 1323 females).

The data were collected during the summer of 2016. All respondents provided informed consent, voluntarily agreed to participate in the study, and were paid a nominal fee of $0.15 USD to incentivize timely completion of the survey. The participants were physically present in the USA at the time they completed the survey. To protect the anonymity of the respondents, the only identifying information collected was the IP address of the device used to complete the survey instrument.

One might point to the non-random and online nature of data collection as a limitation of our study. However, recent research provides compelling evidence that the results of web-based data collection, such as this one, are roughly comparable to those derived from more traditional sampling methods (Gosling et al., 2004; Mortensen and Hughes, 2018). Goodman et al. (2013: 213) conclude that MTurk samples ‘produce reliable results consistent with standard decision-making biases,’ especially if used in conjunction with screening questions. Even though crowdsourced samples admittedly tend to over-represent certain demographic groups like women and younger individuals (Mortensen et al., 2018)—a fact that should be considered when interpreting our results—the consensus nonetheless is that these data are at least as reliable as those collected from traditional methods (Buhrmester et al., 2011; Mortensen and Hughes, 2018). Because crowdsourced samples tend to be more racially, ethnically and socio-economically diverse, they can even be more representative of the population than data collected via traditional, random face-to-face methods (Casler et al., 2013). Despite these numerous strengths, we recognize that online samples are still susceptible to selection bias, and therefore urge some caution in the interpretation of the results.

Tattoo and labor market measures

A key advantage of our dataset is the detailed information on tattoo characteristics. Four measures were used as the explanatory variables in our models. The broadest measure of tattoo status is a binary variable indicating whether the respondent has one or more permanent tattoos of any size (1 = any tattoo; 0 = no tattoo). The other three measures are number of tattoos (count variable; see Figure 1 for a graph of the frequency distribution), one or more ‘visible’ tattoos (binary variable with 1 = visible tattoo; 0 = no tattoo or no visible tattoo), and one or more ‘offensive’ tattoos (binary variable with 1 = offensive tattoo; 0 = no tattoo or no offensive tattoo). We also collected information on percentage of the body covered by tattoos, but most tattooed individuals reported a relatively small percentage covered, and the responses were highly skewed, so we decided not to use this variable.

The key dependent variables are employed (employed = 1; unemployed or not in the labor force = 0), hours worked per week, weeks worked in the past year, annual earnings, weekly rate of pay (calculated) and hourly rate of pay (calculated). To enhance reporting honesty and precision in the survey, we divided annual earnings into 14 mutually exclusive and collectively exhaustive categories, with increments of $5000 (e.g. $0‒$5000), $10,000 (e.g. $80,000‒$90,000), or $50,000 (e.g. $150,000‒$200,000). The top category corresponds to earnings greater than $200,000 per year. For some analyses, we retain the ordered categories and estimate the relationships using ordered probit. This statistical method is an alternative to regression where the dependent variables are ordinal, rather than scale; the estimations are based on maximum likelihood instead of ordinary least squares (Borooah, 2002). To create a quasi-continuous earnings variable, we recoded the responses by taking the midpoint of each category and adding $100,000 (i.e. $200,000 + $100,000 = $300,000) to the minimum of the open-ended top category. This recoding exercise also allows us to construct measures for weekly rate of pay (annual earnings/weeks worked past year) and hourly rate of pay (annual earnings/(weeks worked past year × hours worked per week)).

To investigate whether the three earnings variables (annual earnings, weekly wage, hourly wage) are highly correlated, we prepared a correlation matrix (by gender). We were somewhat surprised to learn that the correlations are not as high as we expected. Specifically, correlation coefficients range from .2217 (hourly wage and annual earnings) to .7603 (weekly wage and hourly wage) for males, and .1492 (hourly wage and annual earnings) to .6196 (weekly wage and annual earnings) for females. Thus, we believe that each of these measures shows a somewhat different form of employee compensation, and analyzing them separately will offer a deeper understanding of the relationships between tattoos, wages and annual earnings.

Control variables

In designing the survey instrument, we took great care to address potential omitted variable bias by including as many relevant controls as possible in our models. The tattoo variables are potentially endogenous because obtaining a tattoo is a behavioral choice that may be significantly correlated with covariates that also predict employment and earnings. Factors that may be correlated with our outcome variables were thus measured and included as control variables in the models. These controls include conventional socio-demographics, health status and risky behaviors. More specifically, we controlled for age, race (white, black, Asian, other), Hispanic ethnicity, marital status (married, separated, divorced, or single), number of children, respondent’s education, father’s education, mother’s education, religiosity, self-reports of overall health status, self-reports of socio-economic status, sexual orientation, whether respondent is a smoker, whether respondent consumes alcohol, whether respondent has been in jail or prison, and whether respondent has ever been diagnosed with a mental health issue. By parceling out the influence of these variables in our models, we are better able to estimate the true effect of body art on labor market outcomes.

Descriptive statistics

Table 1 reports means and proportions for all analysis variables by tattoo status (any or none) and gender. Significance tests (non-parametric Kruskal-Wallis tests for dichotomous and categorical variables, and t-tests for continuous variables) were conducted to determine whether means and proportions are significantly different based on tattoo status. As with the statistical analyses that follow, all significance tests are gender-specific.

Table 1.

Means and proportions for all analysis variables, by gender and tattoo status^a (full sample).

	Men			Women
	Tattoo status			Tattoo status
	All(N = 685)	No(N = 526)	Yes(N = 159)	All(N = 1,323)	No(N = 838)	Yes(N = 485)
Employment status
Employed (%)	76.35	74.90	81.13	66.82	66.23	67.84
Unemployed (%)	14.60	15.78	10.69	11.49	10.86	12.58
Not in labor force (%)	9.05	9.32	8.18	21.69	22.91	19.59
Hours worked per week**	30.56	2936	34.53	24.40	23.97	25.14
Weeks worked past year*	34.42	33.37	37.89	30.02	29.33	31.19
Annual personal earnings ($)^a	36,485	34,929	41,635	25,930	26,516	24,918
Weekly rate of pay ($)^{b ++}	1,252	1,282	1,163	941	1,000	842
Hourly rate of pay ($)^{c ++}	34.79	36.65	29.09	29.40	32.97	23.37
Age**⁺⁺	34.16	34.05	34.51	35.87	37.46	33.13
Race
White (%)	79.56	79.85	78.62	80.35	79.36	82.06
Black (%)	6.86	6.46	8.18	10.36	10.02	10.93
Asian (%)	7.15	8.75	1.89	4.84	6.56	1.86
Other (%)	6.42	4.94	11.32	4.46	4.06	5.15
Hispanic (%)	11.82	10.84	15.09	6.95	6.32	8.04
Marital status
Married (%)*	37.81	35.36	45.91	42.63	42.60	42.68
Separated or divorced (%)	6.86	5.70	10.69	11.19	9.90	13.40
Single (%)**	55.33	58.94	43.40	46.18	47.49	43.92
# of children**⁺	1.66	1.59	1.91	2.09	2.03	2.19
Education
No high school degree (%)	.73	.76	.63	.76	.72	.82
High school degree (%)	12.12	11.03	15.72	9.52	7.64	12.78
Some college (%)⁺	31.82	31.75	32.08	33.18	31.03	36.91
Undergraduate degree (%)	38.39	39.35	35.22	42.03	43.56	39.38
Master’s degree (%)	13.14	13.69	11.32	12.32	14.20	9.07
Professional degree (%)	3.80	3.42	5.03	2.19	2.86	1.03
Father’s education
No high school degree (%)	8.91	9.32	7.55	12.09	12.17	11.96
High school degree (%)*	30.66	27.95	39.62	35.30	33.41	38.56
Some college (%)	18.25	18.44	17.61	17.01	16.83	17.32
Undergraduate degree (%)	28.32	29.85	23.27	21.84	21.48	22.47
Master’s degree (%)	9.64	9.89	8.81	8.16	8.83	7.01
Professional degree (%)	4.23	4.56	3.14	5.59	7.28	2.68
Mother’s education
No high school degree (%)	7.45	7.22	8.18	8.99	9.55	8.04
High school degree (%)	31.24	30.99	32.08	32.80	31.98	34.23
Some college (%)	20.88	20.72	21.38	22.60	21.60	24.33
Undergraduate degree (%)	28.61	29.28	26.42	24.34	24.34	24.33
Master’s degree (%)	9.49	10.08	7.55	8.47	9.67	6.39
Professional degree (%)	2.34	1.71	4.40	2.80	2.86	2.68
Religiosity
Not at all (%)⁺⁺	39.12	38.78	40.25	30.61	27.09	36.70
A little (%)	17.08	17.30	16.35	16.02	15.87	16.29
Some (%)	16.50	16.73	15.72	20.18	19.09	22.06
A lot (%)	18.83	18.25	20.75	22.07	23.87	18.97
Very (%)⁺	8.47	8.94	6.92	11.11	14.08	5.98
Health status
Poor (%)	4.53	4.75	3.77	3.02	2.86	3.30
Fair (%)	22.19	22.62	20.75	18.75	19.81	16.91
Good (%)⁺	37.08	35.93	40.88	44.97	42.00	50.10
Very good (%)	28.61	28.71	28.30	26.83	28.04	24.74
Excellent (%)	7.59	7.98	6.29	6.42	7.28	4.95
Heterosexual (%)⁺⁺	88.91	89.92	85.53	84.73	88.19	78.76
Homosexual (%)	5.55	5.13	6.92	4.31	3.46	5.77
Bisexual (%)⁺⁺	5.55	4.94	7.55	10.96	8.35	15.46
Current smoker (%)**⁺⁺	18.83	14.26	33.96	18.75	13.84	27.22
Current alcohol drinker (%)**⁺⁺	61.90	58.56	72.96	62.51	58.47	69.48
Ever in jail or prison (%)**⁺⁺	15.62	11.60	28.93	7.94	4.06	14.64
Low socioeconomic status (%)⁺⁺	29.34	29.47	28.93	24.79	21.24	30.93
Ever diagnosed mental health issue (%)⁺⁺	20.29	19.20	23.90	32.73	27.33	42.06

Notes: Statistically significant differences between those with and without a tattoo(s) were assessed for both genders (non-parametric Kruskal-Wallis tests for dichotomous and categorical variables, and t-tests for continuous variables). Men: ^*p < .05, ^**p < .01; women: ⁺p < .05, ⁺⁺p < .01

Annual personal earnings were reported in 14 categories. This measure was recoded into a continuous variable by taking the midpoint of each category.

This variable was created as follows: annual personal earnings/weeks worked per year.

This variable was created as follows: annual personal earnings/(weeks worked per year × hours worked per week).

Over 23% of males and almost 37% of females report having at least one tattoo (p < .01). Among men, 76.4% are employed, 14.6% are unemployed, and 9.0% are out of the labor force. The labor market distribution is somewhat different for women in a predictable direction, with 66.8% employed, 11.5% unemployed, and 21.7% out of the labor force. Men also have greater labor supply and higher earnings than women when considering the average hours worked per week (30.6 vs 24.4), average weeks worked per year (34.4 vs 30.0), average annual earnings ($36,485 vs $25,930), average weekly rate of pay ($1,252 vs $941), and average hourly rate of pay ($34.79 vs $29.40). Descriptive statistics for all of the other analysis variables can be found in Table 1. Many of the means and proportions show statistically significant differences between those groups with and without a tattoo, regardless of gender.

Empirical models

We examine six labor market outcome variables (employment status, hours worked per week, weeks worked per year, annual earnings, hourly rate of pay, weekly rate of pay). For consistency and comparability to models and results in French et al. (2016), we constructed the measures similarly. Employment conditional on labor force participation (i.e. those employed or actively seeking employment) is a binary variable, so we estimate this relationship with probit models and report marginal effects. All other variables are continuous (also conditional on labor force participation), so we estimate these models using robust regression, a hybrid form of ordinary least squares that down-weights outlier observations (Verardi and Croux, 2009). The original earnings variable (i.e. prior to recalculation to form a quasi-continuous variable) is ordered with 14 categories. Thus, we also estimate the ordered earnings variable with ordered probit. Because earnings in observational datasets tend to be skewed, we follow the common practice of analyzing the natural logarithm of earnings (Robins et al., 2011). Thus, coefficient estimates have the interpretation of an approximate percentage change (semi-elasticity).

Each of the labor market outcome variables has eight specifications, including four for each gender. The first gender-specific model has ‘any tattoo’ as the key regressor. Results from this model can be directly compared to those from French et al. (2016) because that was the only tattoo measure they used in their study. The second model replaces the binary variable for having one or more tattoos with a count measure for the number of tattoos. This count variable ranges from 0 to a top-coded value of 20 (unconditional mean = .867; conditional (on having at least one tattoo) mean = 3.736) for men, and 0 to a top-coded value of 20 (unconditional mean = 1.317; conditional (on having at least one tattoo) mean = 3.594) for women. The key regressor in the third model is a binary variable signifying the presence of one or more visible tattoos (unconditional proportion = .108 for men and .212 for women; conditional (on having at least one tattoo) proportion = .465 for men and .579 for women). Finally, the last model includes a binary variable for the presence of one or more offensive tattoos (unconditional proportion = .018 for men and .011 for women; conditional (on having at least one tattoo) proportion = .075 for men and .029 for women). All models for employment status, weeks worked per year, hours worked per week, weekly rate of pay and hourly rate of pay include the core set of control variables (age, race, ethnicity, marital status, number of children, education, father’s education, mother’s education, religiosity, health status, sexual orientation, smoking status, drinking status, criminal justice history, low socioeconomic status and ever diagnosed with a mental health issue) presented in Table 1. All models for annual earnings include the same core set of control variables along with weeks worked per year and hours worked per week to control for labor market effort.

We write the fully-specified model for log earnings as:

\ln (E a r n i n g s) = β_{0} + β_{t} T + β_{w} W + β_{h r} H R + X β_{x} + H β_{h} + Z β_{z} + μ,

(1)

where ln(Earnings) is the natural logarithm of annual personal earnings, T is one of the four tattoo variables (any, number, visible, offensive), W is weeks worked per year, HR is hours worked per week, X is a vector of socio-demographic variables, H is a vector of health-related indicators, Z is a vector of risky behaviors, and µ is a random error term. All of the other count and continuous outcome variables (natural log for hourly rate of pay and weekly rate of pay; unadjusted counts for hours worked per week and weeks worked past year) are estimated with an identical empirical model, except that weeks worked per year and hours worked per week are not included as independent variables. The only binary outcome is employment status, which is estimated with probit and follows a similar specification. Because earlier research has shown that gender differences are present with labor market discrimination, labor supply and earnings (French et al., 2009; Hamermesh and Biddle, 1994; Robins et al., 2011), we analyze men and women separately.

Results

The structure for presenting empirical results is identical for each of the six labor market outcomes. Given the abundance of empirical specifications, we only report coefficient estimates (marginal effects) and corresponding standard errors for the tattoo variables. The top panel of each table contains the estimates for men and the bottom panel applies to women. The full set of probit estimation results predicting employment conditional on labor force participation (both genders) for tattoo status is presented in Appendix Table A (available online as supplementary material).

The full set of robust regression estimation results predicting log (annual earnings) conditional on labor force participation (both genders) for tattoo status is displayed in Appendix Table B (available online as supplementary material).

All of the other estimation results not formally presented in tables are available upon request from the authors.

Table 2 contains the first set of results from our empirical models—employment status conditional on labor force participation. For men, only one (any tattoo) of the four tattoo variables is significantly related to conditional employment (p < .05). Somewhat surprisingly, the relationship is positive. Quantitatively, having one or more tattoos is associated with a .061 higher probability (7.3% relative to the mean) of being employed. Conversely, none of the tattoo regressors for employment status is statistically significant for women. In addition, none of the results is qualitatively different for either gender when we examine employment status for the full sample rather than the conditional (on labor force participation) sample.

Table 2.

Selected probit estimation results predicting employment conditional on labor force participation.

Men (N = 623)
Tattoo variable	Any tattoo	Number of tattoos	Visible tattoo(s)	Offensive tattoo(s)
Sample proportion for dependent variable	.839	.839	.839	.839
Coefficient estimate	.378*	.008	.513	‒.538
(Standard error)	(.193)	(.026)	(.273)	(.478)
[Marginal effect]	[.061]	[.001]	[.007]	[‒.132]
Women (N = 1,036)
Sample proportion for dependent variable	.853	.853	.853	.853
Coefficient estimate	.104	.024	.155	.007
(Standard error)	(.114)	(.021)	(.131)	(.493)
[Marginal effect]	[.021]	[.005]	[.030]	[.001]

Notes: Dependent variable in all specifications is employed (part-time or full-time) conditional on labor force participation (i.e. those who are employed or actively seeking employment). Coefficient estimates, corresponding standard errors in parentheses, and marginal effects in brackets are from probit estimation. All specifications control for age, race, ethnicity, marital status, number of children, education, father’s education, mother’s education, religiosity, health status, sexual orientation, smoking status, drinking status, criminal justice history, low socioeconomic status and ever diagnosed with a mental health issue.

Statistically significant, p ≤ .05.

Table 3 contains selected estimation results (robust regression) for weeks worked during the past year conditional on labor force participation. For both men and women, none of the tattoo measures is significantly related to weeks worked during the past year. When estimating the core models with Poisson or negative binomial instead of robust regression, or the full sample rather than the conditional sample, the results are unchanged.²

Table 3.

Selected robust regression results predicting weeks worked per year conditional on labor force participation.

Men (N = 623)
Tattoo variable	Any tattoo	Number of tattoos	Visible tattoo(s)	Offensive tattoo(s)
Sample mean for dependent variable	37.85	37.85	37.85	37.85
Coefficient estimate	.098	.026	.068	‒.450
(Standard error)	(.502)	(.078)	(.595)	(1.487)
Women (N = 1,036)
Sample mean for dependent variable	38.33	38.33	38.33	38.33
Coefficient estimate	.703	.074	.083	2.581
(Standard error)	(.403)	(.071)	(1.08)	(1.947)

Notes: Dependent variable in all specifications is weeks worked per year conditional on labor force participation (i.e. those who are employed or actively seeking employment). Coefficient estimates are marginal effects from robust regression estimation, and corresponding standard errors are reported in parentheses. All specifications control for age, race, ethnicity, marital status, number of children, education, father’s education, mother’s education, religiosity, health status, sexual orientation, smoking status, drinking status, criminal justice history, low socioeconomic status and ever diagnosed with a mental health issue.

None of the estimates is statistically significant, p ≤ .05.

Table 4 contains selected estimates for hours worked per week (robust regression), conditional on labor force participation. For these specifications, the estimates for any tattoo and number of tattoos are positive and statistically significant at p < .05 or better. Among men, having a tattoo is associated with 3.347 additional hours worked per week (p < .05). The estimate for number of tattoos is .751 (p < .01). The findings are similar for women. The estimates for any tattoo and number of tattoos are 2.531 (p < .05) and .462 (p < .05). Lastly, the magnitudes and statistical significance of these estimates change very little when estimating the core models with Poisson or negative binomial instead of robust regression, or the full sample rather than the conditional sample.³

Table 4.

Selected Robust regression results predicting hours worked per week conditional on labor force participation.

Men (N = 623)
Tattoo variable	Any tattoo	Number of tattoos	Visible tattoo(s)	Offensive tattoo(s)
Sample mean for dependent variable	33.60	33.60	33.60	33.60
Coefficient estimate	3.347*	.751**	.119	3.892
(Standard error)	(1.666)	(.260)	(.060)	(4.946)
Women (N = 1,036)
Sample mean for dependent variable	31.16	31.16	31.16	31.16
Coefficient estimate	2.531*	.462*	1.096	.645
(Standard error)	(1.154)	(.203)	(1.387)	(5.590)

Notes: Dependent variable in all specifications is hours worked per week conditional on labor force participation (i.e. those who are employed or actively seeking employment). Coefficient estimates are marginal effects from robust regression estimation, and corresponding standard errors are reported in parentheses. All specifications control for age, race, ethnicity, marital status, number of children, education, father’s education, mother’s education, religiosity, health status, sexual orientation, smoking status, drinking status, criminal justice history, low socioeconomic status and ever diagnosed with a mental health issue.

Statistically significant, p ≤ .05; **statistically significant, p ≤ .01.

The next set of estimates in the sequence pertains to the natural log of (recoded) annual earnings conditional on labor force participation (Table 5), which was estimated with robust regression. We also estimated the original categorical measure of annual earnings using ordered probit (Table 6). Regardless of whether we analyze the continuous or categorical measure of earnings, none of the estimates is statistically significant. In unreported analyses (available upon request), we ran regressions for hourly wage as well as weekly wage. Again, the estimates are non-significant. Moreover, the results are nearly identical when the core models for earnings are re-estimated with the full sample rather than the conditional (on labor force participation) sample, and conditional on employment rather than conditional on labor force participation.⁴ Considering the estimates collectively, these results strongly suggest that any number or type of tattoo(s) is entirely unrelated to labor market compensation in any form.

Table 5.

Selected robust regression results predicting ln(Earnings) conditional on labor force participation.

Men (N = 623)
Tattoo variable	Any tattoo	Number of tattoos	Visible tattoo(s)	Offensive tattoo(s)
Sample mean for annual earnings	40,116	40,116	40,116	40,116
Coefficient estimate	.099	.004	.139	.017
(Standard error)	(.083)	(.013)	(.113)	(.247)
Women (N = 1,036)
Sample mean for annual earnings	33,113	33,113	33,113	33,113
Coefficient estimate	‒.095	‒.009	‒.003	.378
(Standard error)	(.067)	(.012)	(.078)	(.324)

Notes: Dependent variable in all specifications is the natural logarithm of annual earnings conditional on labor force participation (i.e. those who are employed or actively seeking employment). Coefficient estimates are marginal effects from robust regression estimation, and corresponding standard errors are reported in parentheses. All specifications control for hours worked per week, weeks worked per year, age, race, ethnicity, marital status, number of children, education, father’s education, mother’s education, religiosity, health status, sexual orientation, smoking status, drinking status, criminal justice history, low socioeconomic status and ever diagnosed with a mental health issue.

None of the estimates is statistically significant, p ≤ .05.

Table 6.

Selected ordered probit estimation results predicting annual earnings conditional on labor force participation.

Men (N = 623)
Tattoo variable	Any tattoo	Number of tattoos	Visible tattoo(s)	Offensive tattoo(s)
Coefficient estimate (Standard error)	.066 (.109)	‒.009 (.018)	.108 (.150)	.351 (.336)
Women (N = 1,036)
Coefficient estimate (Standard error)	‒.044 (.076)	‒.007 (.013)	‒.018 (.088)	‒.006 (.378)

Notes: Dependent variable in all specifications is annual earnings (14 mutually exclusive and collectively exhaustive categories) conditional on labor force participation (i.e. those who are employed or actively seeking employment). Coefficient estimates are reported, and corresponding standard errors are in parentheses. Sample includes respondents who were employed part-time or full-time. All specifications control for hours worked per week, weeks worked per year, age, race, ethnicity, marital status, number of children, education, father’s education, mother’s education, religiosity, health status, sexual orientation, smoking status, drinking status, criminal justice history, low socioeconomic status and ever diagnosed with a mental health issue.

None of the estimates is statistically significant, p ≤ .05.

The full set of probit estimation results predicting employment conditional on labor force participation (any tattoo) is reported in Appendix Table A (available online as supplementary material).

The first column applies to men and the second column is for women. For men, the statistically significant predictors are any tattoo (positive), other non-white race (negative), and number of children (positive). More variables are significant for women, including education (positive), somewhat religious (negative), health status (positive), bisexual (negative), current alcohol drinker (positive), and ever in jail or prison (negative).

Appendix Table B (available online as supplementary material) contains the full set of robust regression estimation results predicting ln(Earnings) conditional on labor force participation. Coefficient estimates for most of the variables align with conventional human capital theory, and many are statistically significant—for example, hours worked per week and weeks worked per year for both genders (positive), Asian for men (positive), single for women (negative), father’s education (professional degree) for women (positive), bisexual for women (negative), ever in jail or prison for men (negative), and low socioeconomic status for women (negative).

Discussion and conclusions

Overall, these results suggest that tattoos are not significantly associated with employment or earnings discrimination. This finding endures when considering measures of whether one has a tattoo, number of tattoos, whether the tattoos are visible, and whether they are offensive. Not only did we find no net effect of tattoos on earnings, but some evidence emerged of a slight, yet positive, effect of tattoos on labor supply and, for men at least, on employment status. Numerous sensitivity analyses and robustness checks confirm that the core results are stable to alternative variable definitions, estimation techniques and sample construction. The general absence of a ‘tattoo effect’ is consistent with findings from French et al. (2016) and Dillingh et al. (2016), but is surprising in light of the numerous studies pointing to a high level of perceived discrimination against tattooed job applicants and employees (Arndt and Glassman, 2012; Arndt et al., 2016; Bekhor et al., 1995; Brallier et al., 2011; Dean, 2010; Doleac and Stein, 2013; Karl et al., 2016; Larsen et al., 2014; Miller et al., 2009; Swanger, 2006; Timming, 2015; Timming et al., 2017).

This apparent disconnect between perceived discrimination and actual discrimination against tattooed job applicants and employees is something of a mystery, although the ‘actual-vs-perceived’ phenomenon is not, of course, unique. Most social science researchers can point to a myriad of social situations where inflated beliefs fail to correspond to reality. For example, Hargittai and Shafer (2006) found that perceptions of women’s IT skills are significantly lower than their actual IT skills. Martens et al. (2006) found that college students overestimated the level of alcohol consumption, drug use and sexual behavior among their peers. Quillian and Pager (2010) show that most people significantly overestimate the risk of criminal victimization relative to actual crime rates, especially in minority neighborhoods. In short, it would seem that the distorting effect of stereotypes may diminish our ability to accurately perceive the social world. This could be one explanation for the apparent divergence between perceived and actual labor market discrimination against tattooed people.

A second potential explanation for this disconnect is that discrimination against tattooed people exists, but the effects are ‘masked’ within the data and confined only to certain sectors, or types of workplaces. For example, tattoos are much more common in blue-collar jobs than in white-collar ones (Dean, 2010). Industry could thus be seen as a potential confounding factor inasmuch as blue-collar workers, who tend to have more tattoos, also have lower wages vis-a-vis white-collar workers. Moreover, wages are also likely to be affected by consumer attitudes confined to certain industries or sectors. As Arndt et al. (2016) note, tattoos impact customers when they become ‘salient’ in the workplace. Given that tattoos are expected in blue-collar industries, but not white-collar jobs, it is possible, and perhaps even likely, that there are significant wage and employment effects among professional employees. In other words, that our analyses showed no significant effect of tattoos on employment and earnings may well be an artifact of our inability to explore industry effects as such information was not available in the dataset.⁵

A third explanation is that tattoo discrimination was perhaps more prevalent during earlier decades when tattoos were less common, but the overall level of prejudice has attenuated over time. In other words, had there been relevant labor market data as far back in time as the first study on perceived discrimination against tattooed employees and job applicants (Bekhor et al., 1995), it is possible that actual labor market discrimination would have been uncovered in the data. The most plausible reason for why discrimination has diminished in recent years may be linked to the meteoric rise in popularity of tattoos. For example, Polidoro (2014) estimates that, in 2014, 40% of US households had at least one person with a tattoo; in 1999, the corresponding figure was just 21%. If this trend continues, tattooed people will eventually become the majority in society and in the workplace, thus rendering discrimination less likely.

This study has a number of implications for the wider field of work and employment relations. At the most basic level, one could argue that the research makes an incremental contribution to our growing knowledge of the role of body art in the workplace. The overall effects of tattoos appear to be diminishing, quite possibly to the point at which they have become an unremarkable and even mainstream characteristic of the workplace. But such a phenomenon could offer a wider and arguably more significant contribution to the sociological and human resources literatures on equalities and diversity in the workplace.

Özbilgin (2009) argues that at the heart of the equalities research agenda is a strong commitment to human rights and a concern for improving the working lives of disadvantaged people. In other words, equalities researchers typically view themselves to be more than just disinterested actors or value-free scientists, and instead acknowledge that they are driven to redress power imbalances and to resist discrimination, marginalization and oppression. For researchers who cast themselves into this mold, a key takeaway from the present study is that tattooed people, as a social group, are simply not disadvantaged. This study, coupled with French et al. (2016) and Dillingh et al. (2016), provides yet another indication that tattooed job seekers and employees face no discrimination in the labor market and, in fact, may even enjoy some workplace benefits vis-a-vis their non-tattooed counterparts. The same cannot be said of groups like, for example, women, the disabled, and racial and ethnic minorities, many of whom continue to suffer from employment and wage discrimination (Arulampalam et al., 2007; Blau and Kahn, 2006; Deitch et al., 2003; Fevre et al., 2013; Hoque et al., 2018; Laer and Janssens, 2011). Provided that future research can address the shortcomings of the present study, we posit that it may be more productive to revert back to the study of traditional forms of discrimination that are still very much salient and, as yet, unresolved.

In a similar vein, there are also some corresponding practical implications stemming from this research. Specifically, for those organizations that are genuinely concerned about leveling the playing field so that all employees and job applicants are assessed fairly and objectively, it would appear that body art is not an area requiring much investment in time and other resources. Any effort directed towards equality initiatives, whether through training and development (Pendry et al., 2007) or for more strategic reasons (Armstrong et al., 2010), would be better allocated to groups of people suffering from a meaningful and documented disadvantage. Eradicating disadvantage on the basis of gender, race, disability, sexual orientation and age, among other legally protected traits, should not only be seen as a moral imperative (Kaler, 2001; Noon; 2007), but it has also been proved to be good for business (Herring, 2009).

Research limitations

Collecting original primary data using various measures of tattoo characteristics and labor market outcomes is a distinct strength of the present study. However, several limitations pertaining to data collection and estimation also deserve mention. First, to ensure confidentiality and human subject protection, we did not collect any personal identifying information beyond IP addresses. In other words, our sample represents a cross-section of respondents with no opportunity to form a panel. Thus, we are unable to estimate individual fixed-effects models—or other panel data methods—to examine relationships over time. In a similar vein, we lack information on the temporal ordering of tattoos and labor market outcomes, which raises concerns about potential reverse causality (e.g. labor market experiences might influence decisions on whether to obtain a tattoo and the characteristics therein).

The key threat to identification we face in this study is selection on unobservable characteristics (to the analyst) influencing the desire to acquire a tattoo, what image to imprint, and where to display it. That is, tattoo status may be endogenous if important omitted variables in the labor market outcome models are also significantly correlated with tattoo status. Individuals with certain personality traits (e.g. sensation- and thrill-seeking, substance-using, risk-taking, below average cognitive ability) and mental health problems (e.g. depression and anxiety) may be more likely to obtain a tattoo, and these same characteristics may also affect labor market outcomes. If these traits and other important omitted variables are not included in the empirical models, then the coefficient estimates for the tattoo variables could be biased. Although we collected highly detailed and personal information on survey participants and we included these measures in our empirical models, it is unlikely that we can fully address potential bias from omitted variables.

Instrumental variables estimation is a standard technique to address bias in this regard. This econometric method is appropriate for cross-sectional data, where it is desirable to establish or bolster causal inferences (see Muller et al., 2014). However, such methods require suitable (i.e. strong and valid) instruments for the potentially endogenous variable (tattoo status, in this case). Research by French and Popovici (2011) documents the difficulties in defining and measuring suitable instrumental variables in studies of risky behaviors. To address this omitted-variables concern, we explored the possibility of collecting instrumental variables via our survey instrument. However, we were unable to identify any unambiguously strong instruments for tattoo status that are also unrelated (in a direct way) to labor market outcomes. Instead, we sought to include an extensive set of control variables in our empirical models. Nevertheless, we acknowledge that endogeneity bias stemming from omitted variables remains a possible concern with the analyses, and so the results should be interpreted accordingly.

Although we were unable to identify reliable instruments, we do not believe that this is a serious limitation, especially given that instruments are meant to assist in determining significance and causality when estimated associations are significant yet possibly overstated owing to omitted variables and/or endogeneity bias. Given that our correlational results show no net effect of tattoos on employment and earnings outcomes, we are not making any causality claims in this study. Addressing possible endogeneity via instrumental variables, if such an approach were feasible, would not alter the non-significant findings. The few models in which IVs could potentially have been helpful are those where we found a surprisingly positive relationship between tattoos and labor supply. But again, we are not making any claims that tattoos are the cause of this positive relationship. In sum, because the vast majority of the estimates are non-significant, we believe the lack of instruments is not a major problem.

Another limitation pertains to the crowdsourced nature of the sample. Although we present extensive evidence that such samples typically produce largely representative data (Buhrmester et al., 2011; Casler et al., 2013; Goodman et al., 2013; Gosling et al., 2004; Mortensen and Hughes, 2018; Mortensen et al., 2018), we nevertheless recognize, as noted previously, that selection bias is an omnipresent concern in non-randomly drawn samples. On this basis, we suggest that additional research with larger and perhaps more representative samples may be needed to confirm that tattoos are truly not associated with any labor market disadvantage.

Another limitation has also been alluded to above—the absence of pertinent information in the dataset to control for industry, sector or occupation. Based on previous work (Arndt et al., 2016; Dean, 2010), one might expect a ‘sector effect’ in analysis of the relationships between tattoo status and labor market outcomes. At a minimum, this would likely manifest itself between blue-collar and white-collar jobs inasmuch as tattoos are less prevalent in the latter. Although we did not directly measure sector or industry, we were able to use the respondent’s education, father’s education and mother’s education as proxies for industry, sector and occupation. Of course, these measures are imperfect proxies, but they at least provide some information on the types of jobs that the respondents might select.

Lastly, it is worth noting that only 2% of the sample reported having an offensive tattoo, which constrains our predictions in this area. Furthermore, this variable probably contains some degree of measurement error, given that a particular individual might not consider his or her tattoo to be offensive, even though society at large might deem it so (e.g. someone getting a confederate flag tattoo might argue that it represents Southern heritage and culture, whereas many others will view it as a symbol of racism and oppression). This limitation is, however, inherent to any study of art, including body art.

Direction for future research

Where do we go from here in the study of tattoos in the workplace? As provocative as this may seem, in light of the accumulation of recent evidence showing no significant relationship between tattoos, employment and earnings, we believe that the field is approaching the point at which we can suspend this line of research in favor of the more enduring forms of workplace discrimination. If research findings consistently show that tattooed people suffer no serious labor market disadvantage, then our attention is perhaps better spent investigating the real targets of discrimination.

Supplemental Material

HUM782597_Online_Supplementary_Material – Supplemental material for Are tattoos associated with employment and wage discrimination? Analyzing the relationships between body art and labor market outcomes

Supplemental material, HUM782597_Online_Supplementary_Material for Are tattoos associated with employment and wage discrimination? Analyzing the relationships between body art and labor market outcomes by Michael T French, Karoline Mortensen and Andrew R Timming in Human Relations

Footnotes

Acknowledgements

We would like to thank the Editor and the three anonymous reviewers for helpful suggestions on an earlier version of this manuscript. We also acknowledge Katie Kubicki, Gloria Schmitz and Manuel Alcala for research and administrative support.

Funding

This research received no specific grant from any funding agency in the public, commercial or not-for-profit sectors.

Notes

ORCID iD

Andrew R Timming

Michael T French is a Professor of Health Economics at the University of Miami, USA, with a joint appointment in the Department of Health Management and Policy and Department of Sociology. His research interests and experience include health economics, health policy, program evaluation, human resource economics, and transportation economics. Dr French has published over 180 peer-reviewed scholarly articles in a variety of multidisciplinary professional journals, including American Journal of Public Health, Economic Inquiry, Health Economics, Health Services Research, Journal of Health Economics, Journal of Human Resources, Medical Care and Social Science and Medicine. [Email: mfrench@miami.edu]

Karoline Mortensen is an Associate Professor of Health Management and Policy at the University of Miami Business School, USA. Her research interests include the financing, delivery and organization of the United States’ healthcare system. Her research on health insurance, healthcare utilization, and health policies, including the Affordable Care Act, have been published in journals such as Health Affairs, Health Services Research, Medical Care, Journal of General Internal Medicine and JAMA Internal Medicine. [Email: kmortensen@bus.miami.edu]

Andrew R Timming is Associate Professor of Human Resource Management at the University of Western Australia Business School. He holds a PhD in Economic Sociology from the University of Cambridge, UK. His research centers around three streams: employee selection decision-making, employee voice, and workplace mobbing. He is currently Associate Editor at Human Resource Management Journal and The International Journal of Human Resource Management. He has published in journals such as Human Resource Management, Industrial and Labor Relations Review and European Sociological Review. His Twitter handle is @timminglab. [Email: andrew.timming@uwa.edu.au]

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