How not to demonstrate that income inequality impacts economic growth

Many studies have estimated the relationship between income inequality and economic growth (see here and here, for example). Fewer studies have attempted to estimate a causal relationship between the two variables. Unfortunately though, that's what most of us are really interested in. Does higher inequality experience inhibit economic growth?

Theoretically, the causal relationship is not straightforward. Rising shares of income among the wealthy may hold back consumer demand, because the rich save a higher proportion of their income. That would mean that more unequal countries have lower GDP. Alternatively, governments may respond to inequality by redistribution such as progressive taxation, which reduces work and profit incentives and reduces growth. Or, high or rising inequality may reduce trust in government and undermine institutions that are critical for economic growth. On the other hand, the rich save a higher proportion of their income, and those savings are then used for investment spending, which increases economic growth. And more inequality means that those who succeed will receive very high incomes, creating incentives for entrepreneurship and innovation. So, even if inequality causes economic growth, it is unclear if inequality should cause economic growth to be higher, or lower.

This recent article by Zixiang Qi, Bicong Wang (both Beijing Wuzi University), and Yaxin Wang (Chinese Academy of Social Sciences), published in the American Journal of Economics and Sociology (sorry, I don't see an ungated version online) attempts to establish the causal relationship between inequality and economic growth in the long run, using data from 99 countries over the period from 1980 to 2018. Qi et al. find that there is an inverted-U shaped relationship between inequality and economic growth. That is, economic growth is lowest when inequality is low, and when inequality is high, but higher when inequality is middling). However, there is a major problem with the analysis.

In order to establish a causal relationship, Qi et al. rely on an instrumental variables analysis. Instrumental variables analysis involves finding some variable that is correlated with the endogenous variable (income inequality), but uncorrelated with the dependent variable (economic growth, measured as the growth rate of per capita gross national income). That means that the only effect of the instrument on the dependent variable must be through its effect on the endogenous variable.

Qi et al.'s proposed instrument is the age-dependency ratio. Here's where the problem lies. Population ageing has a direct effect on economic growth. The reason why is explained in this post. In fact, Qi et al. even acknowledge this themselves, when they write that:

...Japan's economy has been in a period of secular stagnation for several decades because of ageing population.

So, Qi et al. should know that their instrument is not a valid instrument, and yet they press ahead and use it. At that point, I think we can safely disregard the rest of their results. It is interesting that they found an inverted-U shaped correlation between income inequality and economic growth. But that is all it is - a correlation. We need better methods to establish a causal relationship, and this paper simply doesn't live up to its promise.

Read more:

• Latest research seems to support the Kuznets hypothesis
• Income inequality and economic growth in Australia
• Is there an S-shaped relationship between inequality and per capita GDP?

Mendelian randomisation doesn't necessarily overturn the alcohol J-curve

The alcohol J-curve is the common empirical finding that moderate drinkers have better health than abstainers, and better health than heavy drinkers (see this post, for example). If you plot the relationship between the amount a person drinks and negative measures of health, the resulting curve is shaped like the letter J (as in that earlier post). However, few of the studies that establish a J-curve relationship demonstrate a causal relationship. That's because it is difficult to randomise people into a level of drinking.

However, a relatively new development in epidemiology is the idea of Mendelian randomisation. People are randomly assigned genes at birth. Some of those genes are associated with alcohol consumption. So, alcohol consumption is (partially) randomly assigned by the assignment of genes. Studies can then use instrumental variables regression (a relatively common technique in economics) to estimate the causal effect of alcohol consumption on a range of health (and other) outcomes.

What happens to the J-curve in these Mendelian randomisation studies? This editorial published in the journal Addiction in 2015 (open access), by Tanya Chikritzhs (Curtin University) and co-authors, summarises the state of knowledge up to that point. They note that there is no J-curve relationship observed in Mendelian randomisation studies, or at least that the results are much more equivocal about its existence, and conclude that:

The foundations of the hypothesis for protective effects of low-dose alcohol have now been so undermined that in our opinion the field is due for a major repositioning of the status of moderate alcohol consumption as protective.

I was recently referred to this editorial during a discussion on the J-curve. Having read a bit more about Mendelian randomisation though, I am not entirely convinced. The problem is that in these Mendelian randomisation studies, the two main assumptions of instrumental variables analysis must be met. First, the instrument (having the gene, or not) must be associated with the endogenous variable (alcohol consumption). That assumption should be relatively easy to meet. A researcher simply searches the literature on genome-wide association studies for some gene that is associated with alcohol consumption. Second, the instrument must only affect the dependent variable (health outcomes) through its effect on the endogenous variable (alcohol consumption), and not directly or through any other variable. This is known in economics as the exclusion restriction.

The exclusion restriction is a difficult to satisfy, in part because it is impossible to test statistically. Instead, most researchers settle for being able to identify an instrument that is 'plausibly exogenous'. That is, they find an instrument that is extremely unlikely to affect the outcome variable directly, or indirectly through any other mechanism than through the exogenous variable. In this case, that would mean identifying a gene that could only possibly affect health outcomes through its effect on alcohol consumption.

And that is the problem here. There is no gene for alcohol consumption. All that genome-wide association studies will identify is genes that are associated with alcohol consumption. Those genes all have some other purpose, and that other purpose may be linked to health outcomes in a way that doesn't involve alcohol consumption. As far as I am aware, the Mendelian randomisation studies to date haven't been able to establish that the gene in question has no other effects on health outcomes. That makes their claims to causality no better than those of the correlational studies that they are supposed to improve on.

Mendelian randomisation is good in theory, but not always in practice. For now, the J-curve lives.

It may be time to reconsider weather variables as instruments

For many years, I was sceptical of instrument variables analysis. I expressed a little of this scepticism in one of my early posts on this blog in 2014. However, by then I was starting to come around to the idea, and encouraging my PhD students to consider using it in their work. However, I may have been shifted a little more back towards scepticism by this new working paper by Jonathan Mellon (West Point).

Mellon focuses on the use of weather variables as instruments, and demonstrates the problems associated with using them. However, before he gets that far, he has a very clear exposition of what instrumental variables entails, which is worth sharing. First, here's Figure 1 from the paper:

Then, the associated explanation:

Endogeneity is one of the most pervasive challenges faced by social scientists. Naively, we might assume the causal relationship between two social science variables 𝑋 and 𝑌 can be estimated by their observed relationship [first panel of Figure 1]... However, social scientists usually doubt this simple picture and believe most variables share unmeasured confounders 𝑈 (second panel). One strategy for conducting causal analysis in the presence of endogeneity is using an instrumental variable 𝑊 that causally affects 𝑋 but is uncorrelated with the error term... One of the most important assumptions for any instrumental variable estimation is the exclusion restriction that 𝑊 is associated with 𝑌 only through its relationship with 𝑋 (i.e. there are no other causal pathways from 𝑊 to 𝑌). The assumed DAG for the IV estimation is shown in figure 1’s third panel...

The fourth panel of Figure 1 also demonstrates a problem, where the instrumental variable W affects some other variable Z, which in turn has a direct effect the outcome variable Y.

Mellon's contribution in this paper is to draw attention to the fact that weather variables (mainly rainfall, but also other variables like temperature, wind speed or direction, sunlight, or various others) have been used in so many applications as the variable W, that they must surely have effects on almost every outcome variable Y that don't run only through the variable X. It's kind of an obvious point when you think about it, and Mellon uses the results from over 150 papers to illustrate it, concluding that:

Cunningham (2018) argues that a good instrument should have a “certain ridiculousness”. Until the secret endogenous route to causation is explained, the link between the instrument and outcome seem absurd. In a world where Australians and Californians cannot leave their houses for months at a time due to forest fires, and 1-3 billion people are projected to be left outside of historically-habitable temperature ranges... linkages between weather and the social world are just not ridiculous enough.

Mellon uses weather instruments as his example, but the point he is making is broader. We need to be much more critical of the instrumental variables that are employed. He even offers a simple literature-search-based algorithm for determining whether a proposed instrumental variable is likely to fail the exclusion restriction, which can be used alongside the usual theoretical justification for its use. 

Certainly, it is time to reconsider whether weather variables are valid instruments. Only time (and further criticism along the lines that Mellon has advanced) will determine whether we should be equally sceptical of instrumental variables analysis more generally.

[HT: Marginal Revolution]

News coverage and mass shootings in the US

Does widespread media coverage of mass shootings increase the likelihood of future mass shootings? It seems intuitive that the answer could be 'yes'. Perhaps media coverage encourages 'copycat' behaviour. Perhaps, the prospect of fame motivates mass shooters, and regular media coverage provides the avenue to fame (or, rather, infamy). Maybe media coverage simply makes mass shootings seem 'more normal', as a response to some slight. Teasing out which of these explanations is correct is difficult, especially when you consider that the direction of causality isn't even established. Does media coverage lead to more mass shootings (as the theories outlined above suggest), or do more mass shootings simply lead to more media coverage?

Those are the questions that this recent article by Michael Jetter (University of Western Australia) and Jay Walker (Old Dominion University), published in the journal European Economic Review (sorry, I don't see an ungated version online), set out to address. Jetter and Walker obtain data on mass shootings (four or more victims) for the period from 2006 to 2017, from USA Today's Behind the Bloodshed database. To understand the extent of the problem, they highlight that:

...265 (or six percent) of the 4383 sample days from 2006 to 2017 experienced at least one mass shooting, whereas nine days saw two mass shootings.

Jetter and Walker then collect data on television news from the Vanderbilt Television News Archive. They count the number of news segments from ABC World News Tonight (the highest-ranked evening news programme in the US) that contain the terms 'shoot' (including 'shooter' and 'shooting'). They then filter out false positives manually (such as news items about the shooting of a movie). They find 490 news segments on shootings over the 2006 to 2017 period.

Their analysis relies on an instrumental variables (IV) approach, to avoid the reverse causality problem and obtain the causal effect of news on shootings. To achieve this, they need to identify an instrument that affects the amount of news on shootings, but doesn't directly affect the number of shootings. They suggest disasters in other countries, where large numbers of US expatriates live. Jetter and Walker collect data on disasters from the International Disaster Database, limiting the data to countries with at least 50,000 US emigrants. They note that:

In total, we capture 158 such disasters (132 earthquakes, 10 epidemics, and 16 events of volcanic activity) that span 950 days out of our 4383 sample days.

It turns out that disasters are a good predictor of shooting news (because more disaster news leaves less room in the news broadcast for shooting news). In their IV analysis, Jetter and Walker find that shooting news is:

...a positive, statistically significant, and quantitatively powerful predictor of mass shootings. The corresponding magnitude indicates a one standard deviation increase in shooting news (0.389) translates to an increase in the number of shootings by approximately 73% of a standard deviation.

Now, looking over the time after shooting news, they find that:

The derived coefficients decrease in magnitude and eventually turn statistically indistinguishable from zero after 3-4 weeks.

So, news coverage of shootings causes an increase in mass shootings, and the effect lasts for up to 3-4 weeks. The next question is, why? Jetter and Walker look further into the data, and find no causal relationship from news coverage to murder more generally. That rules out salience, or that shootings are seen as 'more normal' after news coverage of shootings. They find that the mass shootings are more likely to happen on or after the anniversary of other infamous mass shootings, which suggests a behavioural contagion (or 'copycat') effect. Finally, they find that mass shootings are no less likely to happen on days where there would be predictably less change of news coverage (such as the dates of the Super Bowl, Olympics, Academy Awards). That would seem to rule out fame as a significant motivator, since a mass shooter who wants to be famous would probably want to avoid those dates, and yet they don't. So, Jetter and Walker conclude that:

Taken together, the results... are consistent with a behavioral contagion model...

Mass shooters are copycats. And then, in terms of policy implications:

First, our results advise journalists to report less on mass shootings... Second, our results also explain (at least in part) why shootings sometimes cluster in short intervals... Thus, police and other security forces may be well advised to be alert on and after days of heightened media coverage of mass shootings.

In the Waikato Economics Discussion Group a couple of weeks ago, we discussed this paper. We decided you couldn't really replicate this analysis for New Zealand, as (thankfully) mass shootings are very rare. However, one student made mention of ram raids, which have attracted massive attention in the media, this year in particular (for example, see here). Is media coverage of ram raids driving up the number of ram raids in New Zealand? The arguments are very similar to those in the Jetter and Walker article. Whether ram raids are driven by media coverage is an interesting question, and one that may be well worth following up on in an Honours or Masters research project.

Social disorganisation and crime over two centuries

Social disorganisation theory is the idea that differences (or changes) in family structures and community stability are a key contributor to differences (or changes) in crime rates between different places (or times). It suggests that neighbourhoods that are more unstable (higher social disorganisation) will have higher crime rates than neighbourhoods that are less unstable (lower social disorganisation), ceteris paribus (holding everything else constant). It also suggests that if neighbourhoods become more unstable over time, crime rates will increase, ceteris paribus. I've mostly encountered social disorganisation theory in relation to the effect of alcohol outlets on crime. In that context, things become tricky, because alcohol outlets tend to locate in more unstable (higher social deprivation) neighbourhoods, which may also have higher crime because of social disorganisation. So, disentangling the effects of alcohol outlets from the effects of social disorganisation more generally is difficult.

The broader literature on social disorganisation theory faces issues as well, because of potential reverse causation and endogeneity. If you want to test the effect of neighbourhood instability on crime, you have to recognise that not only can instability cause crime, but crime can cause instability. Finding ways of dealing with these issues is important.

So, I was interested to read this recent article by Zeresh Errol (Monash University), Jakob Madsen (University of Western Australia), and Solmaz Moslehi (Monash University), published in the Journal of Economic Behavior and Organization (sorry, I don't see an ungated version online). They use annual data covering the period 1840 to 2018 for 16 countries: Australia, Belgium, Canada, Denmark, Finland, France, Germany, Ireland, Italy, Japan, the Netherlands, Norway, Sweden, Switzerland, the U.K. and the U.S. Their data includes crime rates (per 100,000 population), family structure (proxied by the divorce rate and the share of out-of-wedlock births), community structure (proxied by the urbanisation rate), GDP per capita, and the proportion of the population aged 15-29 years. The crime rates are disaggregated into property crime, violent crime, homicide, robbery and assault. Errol et al. then look at the relationship between the family structure and community structure variables and crime rates (controlling for the other variables, along with country and time fixed effects).

However, remember that endogeneity is a problem here for the family structure variables, so any simple regression analysis is not going to tell us about the causal relationship between family structure and crime. Errol et al. solve this problem using instrumental variables analysis. Essentially, this involves finding an instrument that affects the endogenous variable (divorce or out-of-wedlock birth rate), but has no direct effect on the outcome variable (crime rates). In a unique twist to this paper, Errol et al. use the weighted average of the family structure variables in all other countries as instruments for the family structure variables in country i. For example, for Australia's divorce rate, they use as an instrument the weighted average of the divorce rates in all other countries. The weighted average of other countries' rates is a valid instrument because divorce rates should be related across countries, but the divorce rate in Australia should not exert any effect on the crime rate in Belgium (or any other country). You can tell a similar story for out-of-wedlock birth rates.

Now, rather than using the straight average of all other countries, Errol et al. use a weighted average, where the weights are based on the linguistic distance between the countries. So, data from countries where the main language is more similar will have a greater weight in the calculation of the average. This is quite an exciting aspect of the article to me, because it relates closely to some ongoing work I have been doing on using cultural distance measures in new and exciting ways (more on that in future posts).

Looking at the IV regression results, Errol et al. run separate regressions for the five crime rates, and separately using the divorce rate and the out-of-wedlock birth rate as their proxy for family structure. Across these various models, they find that:

...the coefficients of Div and Owed are significantly positive in seven of the ten cases, where two of the insignificant coefficients pertain to homicide.

In other words, higher divorce rates and out-of-wedlock birth rates cause an increase in crime rates. The size of the coefficients is a little difficult to interpret, given that what Errol et al. report is a coefficient that sums several lagged values. However, they do seem to be meaningful in size, given that Errol et al. note for the ordinary least squares (not IV) regression, that:

Based on the coefficients of the 10-year first difference estimates of Div (Owed), a one standard deviation increase in Div (Owed), is associated with a 15.4(1.8) and 174.4(153.3) percentage point increase in the rates of violent crime and property crime, respectively...

So, this paper demonstrates the important of social disorganisation in understanding differences in crime rates over an extremely long time period. However, it also illustrates a potentially fruitful way of constructing instruments for instrumental variables analyses, using cultural (or, in their case, linguistic) distance weighted averages. Expect to see more work in the future employing this approach.

Church attendance and crime

Does church attendance reduce crime? A simple causal argument could be made that church attendance affects people's moral judgements and therefore their behaviour, reducing crime. However, attempting to establish whether this is the case is going to be difficult empirically, because it isn't easy to conduct an experiment and people aren't randomly allocated to attend church.

This 2020 paper by Jonathan Moreno-Medina (Duke University) takes a slightly different approach. Moreno-Medina relies on the quasi-experimental variation in church attendance that arises because of the weather. Specifically, people are less likely to attend church when it rains. By looking at the extent to which it rains during the specific time window associated with church services (which Moreno-Medina sets as 9am-1pm on Sundays) and how that affects church attendance, Moreno-Medina has an instrument that he can use to extract the causal impact of church attendance on crime. The rain data comes from hourly observations by NOAA, and the county-level crime data comes from the Uniform Crime Reports, and both datasets cover the period from 1980 to 2016.

In a standard instrumental variables analysis, all of the data belongs to the same dataset and both the first stage and second stage regression models can be run jointly. However, that isn't the case for this paper, which is based on the more-rarely-used two-sample two-stage least squares method. Essentially, Moreno-Medina first runs a regression that predicts church attendance at the county level, based on precipitation at the time of church (PTC) and other control variables. The church attendance data comes from the American Time Use Survey, and Google's Popular Times. He then estimates the reduced form regression model for crime, with PTC as an explanatory variable (and including other control variables). The combination of the reduced form model and the first stage can be used to extract the causal effect of church attendance on crime (which I won't go into detail on here, but it is explained in the paper, as well as in econometrics textbooks such as Angrist and Pischke's Mostly Harmless Econometrics, which I reviewed here). You might be concerned that PTC is correlated with precipitation at other times of the week. Moreno-Medina therefore controls for precipitation at other times as well.

In terms of the key results, he finds that:

...having one more Sunday with precipitation at the time of religious services increases substance-related and ‘white-collar’ yearly crimes by around 0.25%, but I find no effect on more serious offenses such as violent crimes (murder, rape, aggravated assault, and robbery) and property crimes. The implied effect of church attendance shows that an increase of 1% in the attendance rate would reduce drug-related crimes by 0.8%, alcohol-related crimes by 0.66% and white-collar crimes by 0.67%.

The headline results in terms of crime overall are mostly plausible. The effects on alcohol-related or drug-related crimes occur within a short time window, but the effects on white-collar crimes (fraud, forgery, etc.) occur with a lag. A lack of statistically significant effects on violent crimes is consistent with a mechanism where church affects crimes to a much weaker extent for violent crimes than for substance-related or white-collar crimes. Moreno-Medina isn't able to specifically identify the mechanisms by which church attendance reduces crime. However, interestingly:

I characterize the population of compliers (individuals who would not attend church because it precipitated at that time) along some observable characteristics. I find that compliers are much more likely to have at least some post-secondary education, and are more likely to be young adults and male. While precipitation decreases average attendance to church, I show that it also increases the probability of engaging in leisure activities at home, but has no effect on other potential confounding activities, such as going to restaurants, outdoors or to the mall.

Given that the results appear to be driven by young males, and 'engaging in leisure activities at home' appears to be what church attendance is substituted for, is this evidence that video game use reduces crime? I'll leave that thought for some further consideration in the future.

[HT: Marginal Revolution]

Video games and class attendance

I've been reading a lot of the research literature lately, on the impact of class attendance on student performance. That relates to writing up some of my own research, based on an experiment I conducted on the ECONS101 class in 2019 (and would have done again in 2020 and this year, if the pandemic hadn't intervened). Anyway, I'll blog about that experiment a bit more in a future post. In this post, I want to talk about this 2018 article I had in my (far too large) to-be-read pile, by Michael Ward (University of Texas at Arlington), published in the journal Information Economics and Policy (ungated version here).

Ward used data from the American Time Use Survey from 2005 to 2012, and looked at the impact of video game playing on the amount of time devoted to class attendance and homework completion, among high school and college students. Ordinarily, this would be a difficult question to get a causal estimate of, as Ward explains:

...a potential negative association between video game play and time devoted to learning may be due to selection of individuals with different preferences for learning as well as a causal result of crowding out. It is possible that marginally performing students are less attached to school and invest less in human capital. Marginally performing students also may have a preference for video game playing. Even without a difference in preferences, they may allocate some of the time freed up from reduced participation in educational activities toward video game playing. In both cases, we would expect a negative correlation between gaming and educational inputs.

In other words, we might observe a negative correlation between video game playing and class attendance because the types of students who play video games are also the types of students who don't attend class anyway, or because students who don't attend class have more time and could therefore use more of that time to play video games (this would be a case of reverse causation).

Ward gets around this problem using instrumental variables analysis. As he explains:

I construct an instrumental variable from video game popularity. When the currently available games are perceived to be higher quality, the utility from playing video games rises. This is a temporary increase because the attractiveness of video games tends to fall quickly with cumulative time played. This temporary increase in marginal utility can result in large swings in the sales of video games from week to week. Thus, week-to-week variation in video game sales will be a valid instrumental variable if it affects time spent playing video games but has no direct effect on time spent on educational activities.

Video game sales can act as an instrument for time spent playing video games because it has no direct impact on time spent studying (in-class or on homework). Ward limits his analysis to weekdays, avoiding the summer holidays and the period between Thanksgiving and the end of the year, he has a sample of 3016 observations of daily time use. Looking at the impact of video game sales for each day (combined with the day before) on study time, he finds that:

A one standard deviation in video game sales leads to an average reduction in class time of about 16 minutes which corresponds to nearly a 10%% [sic] reduction. Video game time is consistently estimated to decrease homework time but this result is smaller and not always statistically significant. The marginal effect of gaming on homework by males is larger than for females but the effect on class attendance is not different from females.

So, video game playing does reduce class attendance, and the reduction is approximately one-for-one (for every additional hour spent playing games, class attendance reduces by an hour). Students aren't trying to make up for it by additional studying outside of class either, so that suggests there is likely a negative impact on student performance (to the extent that class attendance improves student performance). Unfortunately, as much as teachers may wish otherwise, this is the sort of exogenous impact on attendance that it would be difficult for any teacher to combat. Making classes more interactive and encouraging attendance constantly runs up against student preferences for leisure activities.

Finally, Ward's analysis combined all gaming (including console games, computer games, mobile games, and board games [!]). It would be interesting to see if mobile gaming (which is even more prevalent now than it was in the 2005 to 2012 period that Ward's data comes from) has different effects from other gaming. Since, by definition, mobile gaming can be performed anywhere, it might not affect class attendance by as much (although it might affect the extent to which students pay attention in class!). Unfortunately, the time use data doesn't disaggregate gaming further, so it will take a whole other study to answer that question.

Online social networks, social capital, and wellbeing

In economics, capital is essentially defined as a collection of resources that an individual uses to produce goods or services (even if those goods or services are not traded in markets). Some types of capital are obvious, such as machinery or tools (physical capital), or financial wealth (financial capital). Others are a little less obvious, like the stock of human capital (our knowledge, training, and experience, etc.) and natural capital (land, air, water, biodiversity, etc.). Then there is social capital - the social relationships that we have with other people. Social capital is the most difficult to measure (even more difficult than natural capital), but typically we measure it in terms of the number of relationships, and the quality of those relationships, and in terms of quality, we often use the degree of social trust as one measure.

All of that is a long-winded way of talking about the value of online social networks (which is a topic I have discussed before - see the links at the end of this post). In theory, social networks could increase social capital, because they allow us to increase the number of social relationships. However, social networks could also decrease social capital if, in spite of a larger number of relationships, the quality of those relationships is lower. If a social network has a particularly bad culture, the quality might even be negative (if belonging to the network makes us worse off, holding the number of relationships constant).

How can we understand whether social networks have a net benefit (the increase in relationships outweighs any decrease in their quality) or a net cost (the decrease in quality outweighs the increase in relationships)? One way is to look at subjective wellbeing (or life satisfaction, or happiness), and that's what a lot of studies have done (see the links at the end of the post for a few examples). However, fewer studies have also looked at social capital.

One notable exception is this 2017 article by Fabio Sabatini (Sapienza University of Rome) and Francesco Sarracino (STATEC, Luxembourg), published in the journal Kyklos (appears to be open access, but just in case there is an ungated earlier version here). They use data on around 50,000 people from the 2010-2012 waves of the Italian Multipurpose Household Survey. Subjective wellbeing was measured on a 0-10 scale (which is quite common), but online social network use was measured by the yes/no response to the question: "Did you make use of social networking sites such as Facebook and Twitter in the last 12 months?". Social capital was measured by the number of interactions with friends (quantity), and the dichotomous response to the question: "Do you think that most people can be trusted, or that you can’t be too careful in dealing with people?" (quality).

The problem with most studies of online social networks is that they can't show that using the social network causes a change in subjective wellbeing, because perhaps happier (or less happy) people are more likely to use the online social network, in which case the causality runs in the wrong direction. Sabatini and Sarracino try to get around this by using instrumental variables analysis - essentially they predict people's social network access by looking at whether the area they lived in had access to high-speed broadband (DSL or fibre) or not in 2008 (i.e. two years before the survey), then see if the predicted social network access is related to subjective wellbeing. There are issues with these instruments, which I will come back to shortly. Sabatini and Sarracinofind that there is:

...a significant and negative correlation between the use of SNS [social networking sites] and subjective well-being which is independent from the controls for social capital.

In their instrumental variables analysis, they find that:

...the proxies of social capital are positively and significantly associated with life satisfaction, while the use of SNS has negative and significant coefficients.

Finally, they use structural equation modelling (SEM) to look at the inter-relationships between online social network use, social capital, and subjective wellbeing. They find that:

The SEM analysis suggests that the significantly negative correlation between SNS use and subjective well-being obtained in OLS estimates is not only the result of a direct negative effect, but it also results from the combination of two indirect channels:

1. the negative correlation between the use of SNS and social trust that negatively affects well-being.

2. the positive correlation between the use of SNS and face-to-face interactions that positively affects well-being.

Taken all together, their results show that online social networks reduce subjective wellbeing, but that is because online social network use is associated with lower quality of social capital (lower trust), even though online social network use is associated with greater number of social relationships.

This is a nice paper, because of the combination of several methods of analysis. However, the results aren't as strong as the authors claim. The instruments (DSL and fibre broadband access) are not good instruments, because high-speed internet is not necessary in order to access social networks, and because high-speed internet is also associated with increases in the use of many other internet tools (online video, for example). However, despite that, the results are at least consistent with our theoretical predictions from the start of this post. Of most interest may be that the use of online social networks was associated with more face-to-face interactions, rather than just more online interactions.

More papers in this research area should take account of social capital though, if we really want to understand how online social networks affect subjective wellbeing.

Read more:

• The latest NZ research on social media and mental health is nothing special
• What happens when you disconnect from Facebook?
• Does the Internet make people happier?
• The more you use Facebook, the worse you feel
• Quitting Facebook might make you happier

The 2015 refugee crisis, attitudes towards immigrants, and the effect of immigrants on subjective wellbeing

I've been catching up on a bit of reading related to immigration, refugees, and their effects on the native-born population (see also this earlier post of mine on a related topic). The 2015 refugee crisis in Europe provides an interesting natural experiment to test a number of theories about immigrant assimilation, the impacts of migrants on natives, and attitudes towards migrants. A 2019 article by Dominik Hangartner (ETH Zurich) and co-authors, published in the journal American Political Science Review (open access), looks at the last of those three.

Using survey data from 2,070 residents of the Greek islands, Hangartner et al. look at how exposure to the refugee crisis has affected attitudes. They compare residents of islands that received any refugees during the crisis to residents of islands that did not, and use an instrumental variables approach. Their instrument is the distance of the island to the Turkish coast, which would be expected to affect the likelihood that an island receives refugees, but shouldn't affect attitudes directly (especially after controlling for a bunch of other variables in their analysis). They find that:

...direct exposure to the refugee crisis has statistically and politically meaningful effects on natives’ exclusionary attitudes, preferences over asylum and immigration policies, and political engagement. Exploiting the exogenous variation in refugee arrivals caused by distance to the Turkish coast — our instrument — we find that respondents directly exposed to the refugee crisis experience a 1/4 standard deviation (SD) increase in their anti-asylum seeker and anti-immigrant attitudes as well as a 1/6 SD increase in their anti-Muslim attitudes. Compared to respondents on unexposed islands, they are more likely to oppose hosting additional asylum seekers and to support the ban from school for asylum seekers’ children and are less likely to donate to UNHCR and to sign a petition that lobbies the government to provide better housing for refugees.

In other words, it's all bad news. Looking into the reasons for their results, they can exclude economic concerns:

...because refugees quickly left the islands for other European countries, the usual materialist concerns that immigrants compete with natives over scarce resources such as jobs or welfare benefits... do also not apply in this context.

So, it was the mere exposure to the crisis itself that led to these changes in attitudes. Most worryingly, it appears that these attitudinal changes had some persistence over time, because the survey was conducted in early 2017, nearly a year after the refugee crisis had abated.

Hangartner et al. put their results down to:

The inability of the local and European authorities to effectively manage the refugee flows and provide medical support and sanitary services caused chaotic scenes at the hotspots and sparked concerns about the spread of diseases.

That at least suggests that better handling of the situation could have avoided the worst effects. However, it is speculative, since we don't know what would have happened had the crisis been more effectively dealt with. There are two other conclusions from the research that are also worrying:

Our findings of a uniform effect of exposure to the refugee crisis across the sample suggest that this threat triggered exclusionary reactions not only among those already predisposed against immigration, but also among respondents who otherwise would exhibit inclusionary attitudes and have not voted for (extreme) right-wing parties in the past...

...we find that exposure to large numbers of asylum seekers causes natives to become more hostile not only toward refugees, but also toward economic migrants and Muslims, including native Muslims who have been residing in Greece for centuries.

The effects were generalised in the population, and had negative spillovers on attitudes to other out-groups. It may take some time for these effects to dissipate.

However, not all studies show bad news. This 2014 article by Alpaslan Akay (University of Gothenburg), Amelie Constant (George Washington University), and Corrado Giulietti (Institute for the Study of Labor, Germany), published in the Journal of Economic Behavior & Organization (ungated earlier version here), looks at the impact of immigration on subjective wellbeing (life satisfaction, measured on a 1-10 scale) of native-born Germans. Using 170,000 observations from the German Socio-Economic Panel survey over the period from 1998 to 2009, they find that:

...an increase of one standard deviation in the immigrant share [in the local labour market area] is associated with an increase of 0.142 standard deviations in natives’ [subjective wellbeing]. This is rather a large effect if one considers that the standardized coefficient for being unemployed is −0.112 and for wage is 0.017.

Local unemployment and GDP don't seem to affect the results, so again there isn't an economic (or labour market) explanation for these results. When they dig a bit further, it is satisfaction with housing (and not satisfaction with job, health, or income) that seems to be driving the overall result.

Despite some attempts by the authors to argue otherwise, it isn't clear to me that these results are necessarily causal - perhaps immigrants are simply more likely to move to areas where people are happier. However, the results are at least suggestive, because the natives are happier where there are more immigrants, but the immigrants are not.

It would be interesting to see some further results on subjective wellbeing after the refugee crisis. The Hangartner et al. results suggest a dramatic change in attitudes following the crisis in an area that the refugees are simply transiting through. It would be interesting (and important for policy purposes) to know whether that effect spills over to their ultimate destinations.

[HT for the Hangartner et al. article: Marginal Revolution, back in January 2019]

Read more:

• Which asylum seekers do Europeans want?

Online classes lower student grades and completion

I've written several posts about research papers that compare online education with more traditional classroom learning (see here and here and here). However, those studies were distinctly small scale compared to the study reported in this 2017 article, by Eric Bettinger (Stanford), Lindsay Fox (Mathematica Policy Research), Susanna Loeb (Stanford), and Eric Taylor (Harvard), published in the journal American Economic Review (seems to be open access, but just in case there is an ungated earlier version here). They used data from a large for-profit university in the U.S., including over 230,000 students doing 750 different courses.

Importantly, this paper was able to establish causal estimates of the impact of online delivery on student performance in the course and in subsequent courses, using an instrumental variable strategy. However, first it is worth noting that the particular setting is important:

Each course is offered both online and in-person, and each student enrolls in either an online section or an in-person section. Online and in-person sections are identical in most ways: both follow the same syllabus and use the same textbook; class sizes are approximately the same; both use the same assignments, quizzes, tests, and grading rubrics. The contrast between online and in-person sections is primarily the mode of communication. In online sections, all interaction—lecturing, class discussion, group projects—occurs in online discussion boards, and much of the professor’s lecturing role is replaced with standardized videos. In online sections, participation is often asynchronous while in-person sections meet on campus at scheduled times. In short, the university’s online classes attempt to replicate its traditional in-person classes, except that student-student and student-professor interactions are virtual and asynchronous.

So, the only difference between the online and traditional in-person classes is that the online course is run online (with necessary differences in communication between students and the lecturer). To get at the causal estimates though, Bettinger et al. use the interaction between the distance to the nearest campus (of which there were over 100) and whether the course was offered both online and in-person in that semester. As they explain:

...in the interaction instrument design, the reduced-form coefficient only measures how the slope, between distance and grade, changes when students are offered an in-person class option. The main effect of distance (included in both the first and second stages) nets out any other plausible mechanisms which are constant across terms with and without an in-person option. Parallel reasoning can be constructed for the Offered component of the instrument.

I know that's quite technical, but essentially Bettinger et al. are comparing the outcomes for students who did, and did not, take the online course when it was available to them, knowing that distance is a determinant of whether the students would take the in-person course. I hadn't seen this type of interaction instrument used before, and it's something that might come in handy in some of my other work.

The results that Bettinger et al. find were not surprising to me:

The estimated effect of taking a course online is a 0.44 grade point drop in course grade, approximately a 0.33 standard deviation decline. Put differently, students taking the course in-person earned roughly a B− grade (2.8) on average while their peers in online classes earned a C (2.4). Additionally, taking a course online reduces a student’s GPA the following term by 0.15 points. The negative effect of online course-taking occurs across the distribution of course grades. Taking a course online reduces the probability of earning an A or higher by 12.2 percentage points, a B or higher by 13.5 points, a C or higher by 10.1 points, and a D or higher (passing the course) by 8.5 points...

Basically, it's all bad news for online courses. They also find that the impacts are greatest for those at the bottom of the grade distribution, with statistically insignificant effects on the top three deciles of students. That isn't too much different for the results on flipped classrooms that I have discussed before (see here and here). Students also do significantly worse in future courses (after the online course), and are significantly less likely to be enrolled in the future (they are more likely to drop out).

There are some important take-away messages from this research. First, many universities are progressing towards online delivery, either alongside traditional in-person delivery or in place of it. There may be cost savings to online delivery, but those cost savings need to be carefully weighed up against the worse student outcomes that can be expected from online courses. Second, many students seem to be very keen on signing up for online courses, in preference to in-person classes, probably because of the flexibility that an online course provides. Again, the benefit of flexibility needs to be carefully weighed up against the worse outcome (not just in that course, but in future courses) that would result from taking the online course.

Of course, as Bettinger et al. note in their paper, for some students there is no alternative to online education. However, for those who do have a choice, taking an in-person class may be preferable.

Read more:

• Online vs. blended vs. traditional classes
• Flipped classrooms work well for top students in economics
• Flipped classrooms are still best only for the top students

How the internet affects international migration decisions

In the 1960s, Everett Lee came up with a model of migration decisions (ungated version here) that remains the most widely used theory of what determines peoples' migration decisions. Lee emphasised that there are: (1) push factors - things in the origin that cause people to want to move away, like low wages or high unemployment; and (2) pull factors - things in the destination that cause people to want to move there, like high wages or low unemployment. Push factors can be positive (they make you want to move away), or negative (they make you want to stay), and likewise pull factors can be positive (they make you want to move there) or negative (they make you not want to move there). A third factor has been added to these push and pull factors - facilitating factors, or things that make migration easier, like a simplified visa process.

With the theory out of the way, we can now consider how the internet might affect international migration decisions. The internet facilitates improved communication, including between diasporas and those living in their home country. So, perhaps greater internet access might make migration easier, by increasing the flow of information about how or where to migrate to.

Alternatively, maybe the internet facilitates outsourcing of jobs to previously lower-income countries, increasing job prospects and incomes in the origin, and reducing migration (a negative push factor), or allowing people to work for a firm in the destination country without having to leave the origin country (a negative pull factor). Or maybe the internet facilitates access to goods or services (e.g. Netflix) that previously weren't available in the origin country, improving the quality of life there (again, a negative push factor).

So, it isn't clear from the theory whether the internet would increase, or decrease, international migration. What do the data say? A 2017 article by Hernan Winkler (World Bank), published in the journal Applied Economics Letters (I don't see an ungated version, but it appears to be open access), provides some answer. Winkler estimated a gravity model (which I have previously discussed here) using data from 6072 origin-destination pairs of countries over the period 1990-2010. He found that:

...a 10% increase in internet penetration in the source country is accompanied by a 1% decrease in the stock of migrants born there.

That was based on the simplest model he reported, but other models supported that the internet reduced migration. He also found similar results using an instrumental variables approach, which implies that the results are causal - that is, the internet caused a reduction in international migration. Winkler concluded that:

...the internet may weaken the importance of push factors in the decision to migrate, and that these effects dominate any declines in mobility costs associated with this new technology.

This isn't the last word on this, but it is consistent with a story that the internet is associated with job outsourcing from high-income countries to low-income countries, and weakens the incentives for workers from low-income countries to migrate. Maybe, rather than building a wall, the U.S. should be building out internet infrastructure in low-income countries?

Book review: How Not to Be Wrong

As signalled in a post a few days ago, I've been reading How Not to Be Wrong - The Power of Mathematical Thinking by Jordan Ellenberg, which I just finished. Writing an accessible book about mathematics for a general audience is a pretty challenging ask. Mostly, Ellenberg is up to the task. He takes a very broad view of what constitutes mathematics and mathematical thinking, but then again I can't complain, as I take a pretty broad view of what constitutes economics and economic thinking. The similarities don't end there. Ellenberg explains on the second page the importance of understanding mathematics:

You may not be aiming for a mathematically oriented career. That's fine - most people aren't. But you can still do math. You probably already are doing math, even if you don't call it that. Math is woven into the way we reason. And math makes you better at things. Knowing mathematics is like wearing a pair of X-ray specs that reveal hidden structures underneath the messy and chaotic surface of the world... With the tools of mathematics in hand, you can understand the world in a deeper, sounder, and more meaningful way.

I think I could replace every instance of 'math' or 'mathematics' in that paragraph with 'economics' and it would be equally applicable. The book has lots of interesting historical (and recent) anecdotes, as well as applications of mathematics to a variety of topics as broad as astronomy and social science (as noted in my post earlier in the week). I do feel that mostly the book is valuable for readers that have some sensible background in mathematics. There are some excellent explanations, and I especially appreciated what is easily the clearest explanation of orthogonality I have ever read (on page 339 - probably a little too long to repeat here). Just after that is an explanation of the non-transitivity of correlation that provides an intuitive explanation for how instrumental variables regression works (although Ellenberg doesn't frame it in that way at all, that was what I took away from it).

There are also some genuinely funny parts of the book, such as this:

The Pythagoreans, you have to remember, were extremely weird. Their philosophy was a chunky stew of things we'd now call mathematics, things we'd now call religion, and things we'd now call mental illness.

However, there are some parts of the book that I think Ellenberg doesn't quite get right. For instance, there is a whole section on geometry in the middle of the book that I found to be pretty heavy going. Despite that, if you remember a little bit of mathematics from school, there is a lot of value in this book. It doesn't quite live up to the promise in the title, of teaching the reader how not to be wrong, but you probably wouldn't be wrong to read it.

The debate over a well-cited article on online piracy

Recorded music on CDs and recorded music as digital files are substitute goods. So, when online music piracy was at its height in the 2000s, it is natural to expect that there would be some negative impact on recorded music sales. For many years, I discussed this with my ECON110 (now ECONS102) class. However, in the background, one of the most famous research articles on the topic actually found that there was essentially no statistically significant effect of online piracy on music sales.

That 2007 article was written by Felix Oberholzer-Gee (Harvard) and Koleman Strumpf (Kansas University), and published in the Journal of Political Economy (one of the Top Five journals I blogged about last week; ungated earlier version here). Oberholzer-Gee and Strumpf used 17 weeks of data from two file-sharing servers, matched to U.S. album sales. The key issue with any analysis like this is:

...the popularity of an album is likely to drive both file sharing and sales, implying that the parameter of interest γ will be estimated with a positive bias. The album fixed effects vi control for some aspects of popularity, but only imperfectly so because the popularity of many releases in our sample changes quite dramatically during the study period.

The standard approach for economists in this situation is to use instrumental variables (which I have discussed here). Essentially, this involves finding some variable that is expected to be related to U.S. file sharing, but shouldn’t plausibly have a direct effect on album sales in the U.S. Oberholzer-Gee and Strumpf use school holidays in Germany. Their argument is that:

German users provide about one out of every six U.S. downloads, making Germany the most important foreign supplier of songs... German school vacations produce an increase in the supply of files and make it easier for U.S. users to download music.

They then find that:

...file sharing has had only a limited effect on record sales. After we instrument for downloads, the estimated effect of file sharing on sales is not statistically distinguishable from zero. The economic effect of the point estimates is also small.... we can reject the hypothesis that file sharing cost the industry more than 24.1 million albums annually (3 percent of sales and less than one-third of the observed decline in 2002).

Surprisingly, this 2007 article has been a recent target for criticism (although, to be fair, it was also a target for criticism at the time it was published). Stan Liebowitz (University of Texas at Dallas) wrote a strongly worded critique, which was published in the open access Econ Journal Watch in September 2016. Liebowitz criticises the 2007 paper for a number of things, not least of which is the choice of instrument. It is worth quoting from Liebowitz's introduction at length:

First, I demonstrate that the OS measurement of piracy—derived from their never-released dataset—appears to be of dubious quality since the aggregated weekly numbers vary by implausibly large amounts not found in other measures of piracy and are inconsistent with consumer behavior in related markets. Second, the average value of NGSV (German K–12 students on vacation) reported by OS is shown to be mismeasured by a factor of four, making its use in the later econometrics highly suspicious. Relatedly, the coefficient on NGSV in their first-stage regression is shown to be too large to possibly be correct: Its size implies that American piracy is effectively dominated by German school holidays, which is a rather farfetched proposition. Then, I demonstrate that the aggregate relationship between German school holidays and American downloading (as measured by OS) has the opposite sign of the one hypothesized by OS and supposedly supported by their implausibly large first-stage regression results.

After pointing out these questionable results, I examine OS’s chosen method. A detailed factual analysis of the impact of German school holidays on German files available to Americans leads to the conclusion that the extra files available to Americans from German school holidays made up less than two-tenths of one percent of all files available to Americans. This result means that it is essentially impossible for the impact of German school holidays to rise above the background noise in any regression analysis of American piracy.

I leave it to you to read the full critique, if you are interested. Oberholzer-Gee and Strumpf were invited to reply in Econ Journal Watch. However, instead they published a response in the journal Information Economics and Policy (sorry, I don't see an ungated version online) the following year.  However, the response is a great example of how not to respond to a critique of your research. They essentially ignored the key elements of Liebowitz's critique, and he responded in Econ Journal Watch again in the May 2017 issue:

Comparing their IEP article to my original EJW article reveals that their IEP article often did not respond to my actual criticisms but instead responded, in a cursorily plausible manner, to straw men of their own creation. Further, they made numerous factual assertions that are clearly refuted by the data, when tested.

In the latest critique, Liebowitz notes an additional possible error in Oberholzer-Gee and Strumpf's data. It seems to me that the data error is unlikely (it is more likely that the figure that represents the data is wrong), but since they haven't made their data available to anyone, it is impossible to know either way.

Overall, this debate is a lesson in two things. First, it demonstrates how not to respond to reasonable criticism - that is, by avoiding the real questions and answering some straw man arguments instead. Related to that is making your data available. Restricting access to the data (except in cases where the data are protected by confidentiality requirements) makes it seem as if you have something to hide! In this case, the raw data might have been confidential, but the weekly data used in the analysis are derivative and may not be. Second, as Leibowitz notes in his first critique, most journal editors are simply not interested in publishing comments on articles published in their journal, where the comments might draw attention to flaws in the original articles. I've struck that myself with Applied Economics, and ended up writing a shortened version of a comment on this blog instead (see here). It isn't always the case though, and I had a comment published in Education Sciences a couple of months ago. The obstructiveness of authors and journal editors to debate on published articles is a serious flaw in the current peer reviewed research system.

In the case of Oberholzer-Gee and Strumpf's online piracy article, I think it needs to be seriously down-weighted. At least until they are willing to allow their data and results to be carefully scrutinised.

The ancestral characteristics of modern populations

Economic development is remarkably persistent. There is plenty of research that demonstrates that historical patterns of development are predictive of current patterns of development (for example, refer to the research by Daron Acemoglu and James Robinson, as detailed in their book Why Nations Fail (which is on my long list of books-waiting-to-be-read).

Paola Giuliano (UCLA) and Nathan Nunn (Harvard) have a new dataset that, as far as I can see, has enormous potential for looking at a wide range of questions in development, as well as providing a host of candidate variables for use as instruments in otherwise-unrelated analyses. The development of the dataset is described in an article published earlier this year in the journal Economic History of the Developing Regions (ungated version here). The dataset itself is available from Nathan Nunn's website here.

The journal article by Giuliano and Nunn explains:

We contribute to this line of research by providing a publicly accessible database that measures the economic, cultural, political, and environmental characteristics of the ancestors of current population groups... Specifically, we construct measures of the average pre-industrial characteristics of the ancestors of the populations in each country of the world. The database is constructed by combining preindustrial ethnographic information for approximately 1,300 ethnic groups with information on the current distribution of approximately 7,500 language groups measured at the grid-cell level.

Giuliano and Nunn then go on to describe the dataset, as well as providing illustrations of the data. What particularly caught my eye was a brief analysis they did of the relationship between their historical geographic characteristics (meaning the average ancestral characteristics of populations living in current countries) and current GDP. They find that:

Not surprisingly, being further from the equator is positively associated with real per capita GDP. However, what is more surprising is that the ancestral measure appears to be much more strongly correlated than the contemporary measure. This is particularly striking since we would expect the ancestral measure to be more imprecisely measured than the contemporary measure.

They find similar results for ancestral ruggedness of the land, and ancestral distance from the coastline. The reason these results caught my eye was that it suggests to me that these variables might be suitable instruments for GDP in other analyses (such as when GDP would be endogenous in the particular model you are trying to run. If that was a bit too pointy-headed for you, don't worry. It just suggests that these variables have a lot of potentially cool uses for economists.

[HT: Marginal Revolution]

Binge drinking and earnings: health or social capital?

There is a well-established literature that demonstrates an inverted U-shaped relationship between alcohol consumption and earnings (which Eric Crampton touches on here). I just finished reading this 2010 paper, by Preety Srivastava (Monash University) and published in the journal The Economic Record, which is one of several papers that demonstrates this result (ungated earlier version here).

Effectively, the inverted U-shaped relationship means that heavy drinkers have lower earnings than moderate drinkers. It is easy to see why this would be so, due to the negative health and productivity impacts of being a heavy drinker. However, it also means that abstainers (those who don't drink) also have lower earnings than those who drink moderately.

There are several reasons that are proposed for why this might be. First, there is also an established literature that demonstrates a J-shaped curve of the relationship between drinking and health outcomes (Eric Crampton has many posts on this topic, but this one from 2010 is a good place to start). Moderate drinkers have better health than abstainers, so perhaps they have higher earnings because they are healthier than abstainers. Alternatively, perhaps there are positive networking effects (or improved social capital) associated with moderate drinking. Engaging in moderate drinking with colleagues and peers allows workers to deepen their social networks, allowing them to improve their earnings by having access to better jobs over time. Or perhaps the socialising allows them to signal their commitment to the workplace and their colleagues, which improves their chances of successfully receiving promotions or pay rises.

Srivastava uses data from the 2001 and 2004 waves of the National Drug Strategy Household Survey in Australia, and her results are that:

...an inverted U-shaped relationship is found between drinking and earnings across both male and female workers, with a premium for non-bingers and occasional bingers over abstainers, and an earnings penalty for frequent bingers.

The paper is a little questionable (for technical reasons [*]), but for me it left the biggest question unanswered. Is the wage premium for moderate drinkers a result of better health, or better social capital? This is an important question, because workplace drinking and after-work drinks are becoming less common over time. So, the relationship between drinking and social capital is plausibly weakening over time. So we might expect that, if the wage premium for moderate drinkers is primarily driven by health, the premium would remain robust over time, but if it is primarily driven by social capital, it will probably be declining over time. This is an interesting research question that, as far as I can see, no one has yet adequately addressed.

*****

[*] I also take issue with Srivastava's choice of instrumental variables (for more on instrumental variables, see my post here). She uses three instruments: (1) the price of alcohol (at the State level, which means only six observations for all of Australia, so this instrument is actually dropped from the analysis); (2) whether the person first smoked marijuana before age 16; and (3) whether the person has a tattoo. Instruments are supposed to affect the endogenous explanatory variable (in this case, binge drinking), but not have an effect on the dependent variable (in this case, earnings). However, people who smoke marijuana at a relatively young age or who have tattoos might be less risk averse, and less risk averse people may invest less in human or financial capital (e.g. see here), leading to lower income. So, it isn't clear to me that any of the instrumental variables are valid.

The economic non-impact of malaria on African development

When I was completing my PhD, there were a number of studies based on macroeconomic models that showed significant negative impacts of HIV/AIDS on economic growth and yet econometric studies based on observed HIV prevalence of GDP showed virtually no effect. Some people put the difference down to surplus labour (since AIDS deaths are concentrated among prime age adults who make up the majority of the labour force, if there is surplus labour then losing adults from that age group would have little effect on GDP), but even macroeconomic models with surplus labour tended to show some modest negative impact. So much for macroeconomic models (as we later learned during the Global Financial Crisis)?

So, I was interested to read this forthcoming paper in The Economic Journal (ungated earlier version here) by Emilio Depetris-Chauvin (Pontificia Universidad Católica de Chile) and David Weil (Brown University). In the paper, the authors do a number of really interesting things to evaluate the historical and recent economic (non-)impact of malaria. First, they construct an ingenious and deceptively simple model of malaria prevalence, which is based on the prevalence of the gene that causes sickle cell disease. The sickle cell gene provides protection against malaria deaths in childhood for those who have one copy of the gene, but is fatal for those who have two copies of the gene. So the overall prevalence of sickle cell genes can be used to evaluate the overall burden of malaria in the population. The authors estimate that malaria burden is high:

In areas of high malaria transmission, 20% of the population carry the sickle cell trait. Our estimate is that this implies that historically between 10% and 11% of children died from malaria or sickle cell disease before reaching adulthood. Such a death rate is roughly twice the current burden of malaria in such regions. Comparing the most affected to least affected areas, malaria may have been responsible for a ten percentage point difference in the probability of surviving to adulthood. In areas of high malaria transmission, our estimate is that life expectancy at birth was reduced by approximately five years. In terms of its burden relative to other causes of mortality, malaria appears to have been perhaps about as important historically as it is today.

They then use their measure of malaria burden to evaluate the impact of malaria on African development historically. Strikingly, their measure is positively associated with the log of population density (as a measure of development) at the ethnic group level (for 398 ethnic groups across Africa), even after controlling for geography, access to waterways, climate, cultural clustering, suitability for agriculture, and suitability for tsetse flies. Other measures of development, such as having a large (more than 20,000 population) town in the ethnic group's homeland, complexity of the ethnic group's settlement pattern, and centralisation of power, also have a positive or no relationship with malaria burden. Even after adopting an instrumental variables approach (with malaria suitability as the instrument), they still don't find statistically significant negative effects of malaria burden on African development (see here for more on instrumental variables models), though the effects are sometimes negative and not statistically significant.

Why is there no discernible negative economic impact of malaria on African development, given the high malaria burden and the high resulting mortality? One section of the working paper version of the paper that hasn't made it into the final paper is quite interesting. [*] In that section, the authors note that:

The reason that our estimate of the effect of malaria is so small is two-fold. First, malaria deaths are concentrated at young ages, and second, consumption of young children is low relative to consumption of adults. Putting these together, most deaths from malaria do not, in this model, represent a significant loss of resources to society. In our calculation, deaths beyond age five account for only 1/3 of the reduction in life expectancy due to malaria, but for 2/3 of the economic cost of the disease.

So, because malaria mainly kills young children, society wastes relatively few resources investing in children who die from malaria (and can instead expend those resources on surviving children). So, the economic cost of malaria is relatively slight. I don't know why that part of the analysis didn't make it into the final version of the paper, but I think it is one of the more important insights from this work, as it usefully explains why we might not find any economic impact of malaria in Africa.

*****

[*] Actually, there are a lot of substantial differences between the NBER Working Paper version of the paper and the final accepted publication, which might explain why there was a four-year time delay between the two versions of the paper. I'm glad I read the working paper version first, since otherwise I would have missed some of the greater detail.

The puzzle of newspaper pricing

In the simple economic model of supply and demand, when demand decreases the price decreases (except in some special cases such as when supply is perfectly elastic). Typically, the same holds true for other market structures such as monopoly - when demand decreases, the monopolist's profit-maximising price usually decreases.

That makes the recent experience of newspaper subscriptions increasing in price, in the wake of decreasing demand, somewhat of a puzzle. Fortunately, a 2016 paper by Adithya Pattabhiramaiah (Georgia Tech), S. Sriram (University of Michigan), and Shrihari Sridhar (Texas A&M) unpacks the puzzle for us, and ultimately it rests on the fact that this is a platform market (or a two-sided market) - a market where a firm brings together two sides (e.g. in this case the readers and the advertisers), both of whom benefit by the existence of the platform (the newspaper), and both of whom may (or may not) be charged (in this case, the readers are charged a subscription, and the advertisers are charged for advertising). As Nobel Prize winner Jean Tirole has noted, in platform markets it is common for one of the two sides to subsidise the other. To be more precise, the side of the market with relatively more inelastic demand (or greater willingness-to-pay for access to the platform) will subsidise the side of the market with relatively more elastic demand (or lower willingness-to-pay for access to the platform).

So, one potential explanation for the puzzle of increasing subscription prices for readers in the face of decreasing demand is that the decreasing number of readers reduces the value of advertising in the newspaper, which reduces advertisers' willingness-to-pay for advertising, which in turn reduces the optimal subsidy the newspaper will apply to subscriptions. And it is this explanation that Pattabhiramaiah et al. set out to test.

They use data for 2006-2011 from a top-50 regional newspaper in the U.S., supplemented by microdata from 5565 subscribers, to construct models of: (1) the subscribers' decisions about whether to subscribe (and which of three subscription choices to select); (2) the advertisers' decisions about whether to advertise (and whether to do so in classifieds, display, or inserts); and (3) the newspaper's decision about subscription prices. A bit of background first though:

During the period of our analysis (i.e., 2006-2011), 14% of households in the newspaper’s market subscribed to the focal newspaper...

Conditional on subscribing to the focal newspaper, 72.4% (71.6%) of readers within (outside) the core market opt for the Daily option. The corresponding numbers for the Weekend and Sunday only options are 5.4% (4.4%) and 22.2% (23.9%), respectively...

The Daily option witnessed the steepest price increase of nearly 77%, both within and outside the core market, while prices of the Weekend and Sunday only options also increased by 52% and 38%, respectively...

On average, across the three options, the newspaper’s circulation witnessed steep year-on-year declines within (outside) the core market of between 7-10% (2-6%)...

While display and inserts lost 57.7% and 43.4%, respectively during our analysis period, Classifieds ad revenues experienced the steepest decline of 88.3%...

Between 2006 and 2011, classifieds ad rates at the focal newspaper declined by 66%, possibly as a result of the growing popularity of Craigslist. The rates for display ads and inserts experienced smaller declines of 16.7% and 10.8%, respectively.

So, subscription prices for readers increased (and readership decreased), and advertising rates (the price advertisers pay) decreased and so did advertising revenue. However, that decrease in readership was likely to be both the result of decreased price (and so was the result of a movement along the demand curve), and the result of changing reader preferences to (a decrease in demand, or a shift of the demand curve to the left). This creates an identification problem (which I've written on before, here) - which of the movement along the demand curve or the shift in the demand curve has contributed the most to the change in price? [*]

Pattabhiramaiah et al. then used their model to:

...compare how optimal markups evolved between 2006 and 2011 in each of the three cases: actual markups (computed based on our model parameters), the case where we switch off the decline in readers’ preferences, and the case where we switch off the decline in the incentive to subsidize readers at the expense of advertisers.

They find that:

...within the core market, the decline in readers’ preferences accounted for between 8-21% of the increase in subscription prices. On the other hand, nearly 79-92% of the increase in subscription prices between 2006 and 2011 can be traced back to the decreasing incentive on the part of the newspaper to subsidize readers at the expense of advertisers.

So, their results support the argument that the puzzle is explained by decreasing subsidies from the advertiser side of the platform market to the reader side.

There are two final (statistical) points I want to make about this paper, which may leave us with some concern about the results. The first is illustrated by this quote from the paper:

We find that the correlation between the subscription of the local newspaper and the local subscription of national newspapers is 0.8, suggesting that it is not a weak instrument... Overall, these results suggest that the instruments, along with other exogenous variables, explain 83% of the variation in readership. Compared to the first stage regression with only the exogenous variables, but excluding the instruments, the proposed instrumental variables improve the R-squared by 12-14% for ad rates and 11-15% for readership. Therefore, we contend that we do not have a weak instruments problem.

What the hell? There are actual statistical tests that you can run for testing whether you have weak instruments (Stock and Yogo have a whole chapter on it here), but rather than report the results of those tests they obfuscate instead? On the basis of what they have written, we are left with little idea about whether their instruments do a good job or not (for more on instrumental variables, see my post here). The second issue is somewhat hidden in a footnote:

Our in-sample MAPD ranges between 17.4%-17.8%. The out of sample MAPD range between 12.1%-16.8%.

The MAPD (Mean Absolute Percentage Deviation) is a measure of the error in their model, and it is extremely unusual for a model to show a lower error on data that was held over for validating the model (out-of-sample data) than on data that was used to construct the model (in-sample data). After all, most models are constructed to minimise the in-sample error. So this should leave us a little concerned about their model (or their calculation of MAPD). Or perhaps it's just luck that their data does a better job of predicting the 2010-2011 period than the 2006-2010 period?

[HT: Marginal Revolution]

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[*] Pattabhiramaiah et al. use their data to first eliminate the alternative possibilities of increasing quality of the newspaper leading to an increase in price, or increasing marginal costs leading to an increase in price (in fact, they find that marginal costs actually declined over the period).

Does the Internet make people happier?

Following on from the paper I discussed yesterday about Facebook use being associated with lower measures of wellbeing, I thought this 2013 paper by Thierry Penard (University of Rennes), Nicolas Poussing (INSEAD), and Raphael Suire (University of Rennes), published in the Journal of Socio-Economics, was a good way to follow up (it's open access, but just in case there's an ungated earlier version here).

The paper is titled "Does the Internet make people happier?", and the authors used data from the 2008 European Social Survey (but only for 1332 respondents from Luxembourg). Intensity of internet use is their main variable of interest, which:

...is measured by four dummies: Onlineday+ if the Internet is used several times per day (38%), OnlineDay if it is used only once per day (22.3%), OnlineMonth if it is seldom connected (17.1%), and NoInternet if the individual never uses the Internet (22.6%).

They essentially look at how life satisfaction (measured on a ten-point scale) changes with intensity of internet use. So far, so good. Except for the fact that the data is based on a cross-section, so it's only going to show correlations, the approach seems reasonable. The main problem arises later in the analysis. They find:

...a significant negative relation between the non-use of the Internet and life satisfaction. However, among the Internet users, there is no significant difference between the heavy and light users. This suggests that being deprived of Internet access (i.e. being on the wrong side of the digital divide) has a detrimental effect on the well-being.

These results hold up as they add more explanatory variables to their model, but as soon as they add health and income , their main result becomes only weakly statistically significant. Here's where the analysis becomes problematic. Penard et al. introduction interactions between internet intensity and other variables (age, marital status, gender, sociability, and income), but in those interactions they treat the ordinal variable of online intensity (described above as four categories) as a continuous variable (0,1,2,3). Treating an ordinal variable as continuous is unjustifiable in this case - there isn't any reason to believe that the difference between no internet use (0) and online once a month (1) is the same as the difference between online once per day (2) and online several times per day (3), but that is how it is treated in this case.

Once they add these dodgy variables into their analysis, it makes all of the internet intensity variables statistically significant, and of the expected sign. However, the results can't be believed because the additional variables introduce bias into the analysis.

As an aside, I'm always skeptical when a paper suddenly does one of three things after finding weak or statistically insignificant results in their main analysis: (1) looking at sub-groups or subsets of the data; (2) introducing interaction variables; or (3) quantile regression techniques. I may talk more about those in a later post, but if they weren't part of the original plan they really cry out that the researchers were clutching at straws looking for something to report.

There is further evidence that the initial results by Penard et al. lack robustness, and that comes from their own robustness checks reported in the paper. The authors rightly point out that:

It is possible that omitted variables in the estimated models influence both the intensity of Internet use and well-being, or that people who are more satisfied with their life are more likely to use the Internet (inverse causality).

So, they apply an instrumental variables (IV) analysis (which I've described earlier here). This involves finding a variable that you know affects internet use, but which won't have a direct effect on life satisfaction. Penard et al. use internet use by other family members. [*] Once they run the IV analysis, none of their internet intensity variables are statistically significant (even when they include the dodgy interaction variables).

Overall, despite the title this paper doesn't really contribute much to our understanding of whether internet use makes people happier or not. I'd be interested to know what happens to their analysis if you replaced the dodgy interaction variables with interactions based on the proper categorical variables, but I wouldn't expect it to change much (else they would probably have reported those results instead!).

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[*] If I wasn't feeling generous I would point out that this variable fails the exclusion restriction. If the rest of your family uses the internet, perhaps they don't spend so much time on interacting with you, which could directly affect your life satisfaction (positively or negatively, depending on your family!).

Read more:

• The more you use Facebook, the worse you feel
• Quitting Facebook might make you happier