Ceteris Non Paribus

Ceteris Non Paribus is my personal blog, formerly hosted at nonparibus.wordpress.com and now found here. This blog is a place for me to put the ideas I have, and the stuff I come across, that I’ve managed to convince myself other people would be interested in seeing. See the About page for more on the reasons why I maintain a blog and the origin of the blog’s name.

My most recent posts can be found below, and a list of my most popular posts (based on recent views) is on the right.

Ceteris Non Paribus

Scared Straight or Scared to Death? The Effect of Risk Beliefs on Risky Behaviors

Longtime readers of this blog (or anyone who has talked to me in the past few years) know that I have been working on a paper on risk compensation and HIV. Risk compensation typically means that when an activity becomes more dangerous, people do less of it. If the risk becomes sufficiently high, however, the rational response can be to take more risks instead of fewer, a pattern called “rational fatalism”. This happens because increased risks affect not only the danger of additional acts, but also the chance that you have already contracted HIV based on past exposures. While HIV testing appears to mitigate this problem, by resolving people’s HIV status, a similar logic applies for unavoidable exposures in the future; HIV testing cannot do anything about the sense that you will definitely contract the virus in the future. I test this model used a randomized field experiment in Malawi, and show that rational fatalism is a real phenomenon.

The paper is called “Scared Straight or Scared to Death? The Effect of Risk Beliefs on Risky Behaviors”. I’ve just completed a major overhaul of the paper – here’s a link to the revised version, which is now available on SSRN, and here is the abstract:

This paper tests a model in which risk compensation can be “fatalistic”: higher risks lead to more risk-taking, rather than less. If exposure cannot be perfectly controlled, fatalism arises when risks become sufficiently high. To test the model I randomize the provision of information about HIV transmission rates in Malawi, and use a novel method to decompose the risk elasticity of sexual risk-taking by people’s initial risk beliefs. Matching the model’s predictions, this elasticity varies from -2.3 for the lowest initial beliefs to 2.9 for the highest beliefs. Fatalistic people, who have a positive elasticity, comprise 14% of the population.

I’ve put the up on SSRN to try to get it into the hands of people who haven’t seen it yet, and also because I’m making the final edits to the paper ahead of submitting it to an academic journal. Therefore, feedback and suggestions are warmly welcomed.

I’ve written about previous versions of the paper both on this blog and on the World Bank’s Development Impact Blog.

Randomized evaluations of market goods

Last weekend I was lucky enough to attend IPA‘s second annual Researcher Gathering on Advancing Financial Inclusion at Yale University. My friend and collaborator Lasse Brune presented the proposed research design for a study we are planning with Eric Chyn on using deferred wages as a savings technology in Malawi. Our project expands builds on an earlier paper by myself and Lasse that shows that demand for deferred wages is quite high and that there are potentially-large benefits.

The conference featured lots of great talks, but I particularly liked the one Emily Breza gave. She was presenting early results from a paper called “Measuring the Average Impacts of Credit: Evidence from the Indian Microfinance Crisis” that she is writing with Cynthia Kinnan. (Here is a link to an older version of the paper.) One of the major results of the RCT revolution in development economics is a robust literature showing that microcredit – small loans targeted at the very poor, at below-market interest rates – has very limited economic benefits. This was a fairly surprising result, and at odds with both the priors of microfinance practitioners and previous non-experimental research.

Randomized evaluations of microcredit generally follow the following format. You find an area where microcredit doesn’t exist, and get a firm to expand to that area. But instead of providing it to everyone in the area, you convince the firm to randomly select people to offer the product to.

Breza and Kinnan turn that logic on its head. They instead look at markets that were already actively served by microcredit, where the supply of credit was drastically reduced. This reduction happened because of the 2010 Andhra Pradesh (AP) Microfinance Crisis, where a wave of suicides by indebted people caused the AP state government to ban microcredit in the state. Breza and Kinnan don’t study AP in particular; instead, they exploit the fact that some (but not all) microcredit suppliers had exposure AP through outstanding loans there, which defaulted en masse. This reduced their liquidity sharply and forced them to cut back on lending. So if you happened to live in an area largely served by microcredit firms that were exposed to AP, you suffered a large decline in the availability of microloans.

This clever research design yields effects on economic outcomes that are much larger than those estimated in traditional RCTs.* Is that surprising? I don’t think so, because we are studying market goods – those provided through reasonably well-functioning markets, as opposed to things like primary education in the developing world where markets are limited or non-existent.** Any randomized evaluation of a market good necessarily targets consumers who are not already served by the market.

In an RCT we can get the estimated effect of receiving a good by randomizing offers of the good and using the offer as an instrument for takeup. It’s well-known that these local average treatment effects are specific to the set of “compliers” in your study – the people induced to receive the good by the randomized offer. But usually the nature of these compliers is somewhat nebulous. In Angrist and Evans’ study of childbearing and labor supply, they are the people who are induced to have a third kid because their first two kids are the same sex (and people tend to want one of each). Are those people similar to everyone else? It’s hard to say.

In the context of market goods, however, the compliers have a specific and clear economic definition. They are the consumers who firms find it unprofitable to serve. Here is a simplistic illustration of this point:

Priced Out

These are the subset of all consumers with the lowest willingness-to-pay for the good – so we know that they experience the lowest aggregate benefits from it.*** RCTs can only tell us about their benefits, which are plausibly a lower bound on the true benefits across the population. To learn about the actual average treatment effects, in this context, we need a paper like Breza and Kinnan’s.

So were the randomized evaluations of microcredit even worth doing at all? Absolutely. They tell us about what might happen if we expand microcredit to more people, which is policy-relevant for two reasons. First, the priced-out people are the next group we might think about bringing it to. Second, we have a decent sense that markets are not going to serve them, so it’s up to governments and NGOs to decide do so. That decision requires understanding the incremental benefits and costs of expanding microcredit, as compared with all other potential policies.

A broader conclusion is that any study of a good or product that might be provided by markets needs to confront the question of why it is not being provided already – or, if it is, why it is worth studying the benefits of the product for the subset of people whom markets have deemed unprofitable.

*An exception is another paper by Breza and Kinnan, along with Banerjee and Duflo, which finds some long-run benefits of random microcredit offers for people who are prone to entrepreneurship.
**This is distinct from the concept of public vs. private goods. Education is not a public good per se as it is both excludable and rival, but it is typically provided by the state and hence standard profit motives need not apply.
***Leaving aside Chetty’s point about experienced utility vs. decision utility.


Don't control for outcome variables

If you want to study the effect of a variable x on an outcome y, there are two broad strategies. One is to run a randomized experiment or one of its close cousins like a regression discontinuity or a difference-in-differences. The other is to adjust for observable differences in the data that are related to x and y – a list of variables that I’ll denote as W. For example, if you want to estimate the effect of education on wages, you typically want include gender in Z (among many other things). Control for enough observable characteristics and you can sometimes claim that you have isolated the causal effect of x on y – you’ve distilled the causation out of the correlation.

This approach has led to no end of problems in data analysis, especially in social science. It relies on an assumption that many researchers seem to ignore, which is that there are no other factors that we do not include in Z that are related to both y and x.* That’s an assumption that is often violated.

This post is motivated by another problem that I see all too often in empirical work. People seem to have little idea how to select variables for inclusion in Z, and, critically, don’t understand what not to include in Z. A key point in knowing what not to control for is the maxim in the title of this post:

Don’t control for outcome variables.

For example, if you want to know how a student’s grades are affected by their parents’ spending on their college education, you might control for race, high school GPA, age, and gender. What you certainly shouldn’t control for is student employment, which is a direct result of parental financial support.** Unfortunately, a prominent study does exactly that in most of its analyses (and has not, to my knowledge, been corrected or retracted).

Why is it bad to control for variables that are affected by the x you are studying? It leads to biased coefficient estimates – i.e. you get the wrong answer. There is a formal proof of this point in this 2005 paper by Wooldridge. But it’s easy to see the problem using a quick “proof-by-Stata”. *** I’m going to simulate fake data and show that including the outcome variables as controls leads to very wrong answers.

Here is the code to build the fake dataset:

clear all

set obs 1000
set seed 346787

gen x = 2*runiform()
gen e = rnormal()
gen u = rnormal()

gen y = x + e
gen other_outcome = x^2 + ln(x) + u
gen codetermined_outcome = x^2 + ln(x) + e +u

A big advantage here is that I know exactly how x affects y: the correct coefficient is 1. With real data, we can always argue about what the true answer is.

A simple regression of y on x gives us the right answer:

reg y x
           y |      Coef.   Std. Err.      t    P>|t|     [95% Conf. Interval]
           x |    1.08877   .0564726    19.28   0.000     .9779512    1.199588
       _cons |   -.096074   .0645102    -1.49   0.137    -.2226653    .0305172

If we control for a codetermined outcome variable then our answer is way off:

reg y x codetermined_outcome
                y |      Coef.   Std. Err.      t    P>|t|     [95% Conf. Interval]
                x |  -.6710671   .0712946    -9.41   0.000    -.8109717   -.5311624
codetermined_ou~e |   .4758925   .0157956    30.13   0.000     .4448961    .5068889
            _cons |   1.192013   .0633118    18.83   0.000     1.067773    1.316252

Controlling for the other outcome variable doesn’t bias our point estimate, but it widens the confidence interval:

reg y x other_outcome

            y |      Coef.   Std. Err.      t    P>|t|     [95% Conf. Interval]
            x |   1.084171   .1226962     8.84   0.000     .8433988    1.324944
other_outcome |   .0012741   .0301765     0.04   0.966    -.0579426    .0604907
        _cons |  -.0927479   .1018421    -0.91   0.363    -.2925974    .1071017

Both of these controls cause problems. The real problem is co-determined outcomes – things that are driven by the same unobservable factors that also drive y. These will give us the wrong answer on average, and are terrible control variables. (You also shouldn’t control for things that are the direct result of y, for the same reason). Other outcomes are bad too – they blow up our standard errors and confidence intervals, because they are highly collinear with x and add no new information that is not already in x. The safe move is just to avoid controlling for outcomes entirely.

*This is still true even today, despite the credibility revolution that has swept through economics and also reached the other social sciences in recent years.
**The more your parents support you in college, the less you have to work.
***I picked up the term “proof by Stata” in John DiNardo‘s advanced program evaluation course at the University of Michigan.

You still have to test the results of your evolutionary learning strategy

Ricardo Hausmann argues against RCTs as a way to test development interventions, and advocates for the following approach instead of an RCT that distributes tablets to schools:

Consider the following thought experiment: We include some mechanism in the tablet to inform the teacher in real time about how well his or her pupils are absorbing the material being taught. We free all teachers to experiment with different software, different strategies, and different ways of using the new tool. The rapid feedback loop will make teachers adjust their strategies to maximize performance.

Over time, we will observe some teachers who have stumbled onto highly effective strategies. We then share what they have done with other teachers.

This approach has a big advantage over a randomized trial, because the design can adapt to circumstances that are specific to a given classroom. And, Hausmann asserts, it will yield approaches whose effectiveness is unconfounded by reverse causality or selection bias.

Clearly, teachers will be confusing correlation with causation when adjusting their strategies; but these errors will be revealed soon enough as their wrong assumptions do not yield better results.

Is this true? If so, we don’t need to run any more slow, unwieldy randomized trials. We can just ask participants themselves what works! Unfortunately, the idea that participants will automatically understand how well a program works is false. Using data from the Job Training Participation Act (JTPA), Smith, Whalley and Wilcox show that JTPA participants’ perceived benefits from the program were unrelated to the actual effects measured in an RCT. Instead, they seem to reflect simple before-after comparisons of outcome variables, which is a common mistake in program evaluation. The problems with before-after comparisons are particularly bad in a school setting, because all student performance indicators naturally trend upward with age and grade level.

An adaptive, evolutionary learning process can generate a high-quality program – but it cannot substitute for rigorously evaluating that program. Responding to Hausmann, Chris Blattman says “In fact, most organizations I know have spent the majority of budgets on programs with no evidence whatsoever.” This is true even of organizations that do high-quality learning using the rapid feedback loops described by Hausmann: many of the ideas generated by those processes don’t have big enough effects to be worth their costs.

That said, organizations doing truly effective interventions do make use of these kinds of rapid feedback loops and nimble, adaptive learning processes. They begin by looking at what we already know from previous research, come up with ideas, get feedback from participants, and do some internal M&E to see how things are going, repeating that process to develop a great program. Then they start doing small-scale evaluations – picking a non-randomized comparison group to rule out simple time trends, for example. If the early results look bad, they go back to the drawing board and change things. If they look good, they move to a bigger sample and a more-rigorous identification strategy.

An example of how this works can be found in Mango Tree Educational Enterprises Uganda, which developed a literacy program over several years of careful testing and piloting. Before moving to an initial RCT, they collected internal data on both their pilot schools and untreated schools nearby, which showed highly encouraging results. The results from the first-stage RCT, available in this paper I wrote with Rebecca Thornton, are very impressive.

My impression is that most organizations wait far too long to even start collecting data on their programs, and when the results don’t look good they are too committed to their approach to really be adaptive. The fundamental issue here is that causal inference is hard. That’s why it took human beings hundreds of thousands of years to discover the existence of germs. Social programs face the same problems of noisy data, omitted variables, strong time trends, and selection bias – and arguably fare even worse on those dimensions. As a result, no matter how convincing a program is, and how excellent its development process, we still need randomized experiments to know how effective it is.


Liquidity constraints can be deadly

My friend and coauthor Lasse Brune sent me FSD Kenya‘s report on the Kenya Financial Diaries project.  Much of the report, authored by Julie Zollman, confirms that what we already knew to be true for South Africa’s poor (based on the excellent book Portfolios of the Poor) also holds for low-income people in Kenya. I was struck, however, Zollman’s description of the stark consequences Kenyans face if they are unable to access financial markets:

We observed important delays – in some cases resulting in death – from respondents’ inability to finance emergency health spending. In some cases, the financial barriers were substantial – above KSh 20,000 – but in many cases, important delays in treating things like malaria and other infections stemmed from only very small financial barriers, below KSh 500.

500 shillings is just under five US dollars at market exchange rates. Even in the context of the financial lives of the study’s respondents, this seems to be an entirely manageable sum. For the average respondent 500 shillings is less than a third of monthly per-person income. FSD’s poorest respondents, who earn 221 shillings a month, should still be able to afford this cost over the course of a year; it represents 19% of their total budget. That is an amount they should be able to borrow and pay back, or possibly even to save up. Certainly this would be achievable in the developed world.

However, Kenya’s poor are desperately liquidity-constrained:

[E]ven if household income and consumption were steady from month to month, families could still be vulnerable if they could not increase spending to accommodate new and lumpy needs. A quarter of all households experienced actual hunger during the study and 9% of them experienced it during at least three interview intervals. Thirty-eight per cent went without a doctor or medicine when needed and 11% of households experienced this across three or more interview intervals.

Some of my own work (cowritten with Lasse) contributes to an extensive literature that documents the economic costs of liquidity constraints in Africa. These are important, but we should bear in mind that an inability to access credit or savings can also literally be the difference between life and death.

Is it ethical to give money to the poor? Almost certainly

GiveDirectly, the awesome charity that gives cash directly to poor people in developing countries, is back in the news. This time, they are getting attention for a study that uses the random variation in individual income provided by their original experiment to study whether increases in in the wealth of others harm people’s subjective well-being. This is an assumption that underlies a surprisingly popular theory that posits that increases in inequality per se have a direct impact on people’s health.* The most popular formulation of that theory says that inequality raises stress levels, which in turn cause poor health. This theory relies on inequality having a direct effect on stress and other measures of subjective well-being. Given how popular the stress-based theory is, there is surprisingly little evidence of this core claim.

Enter Haushofer, Reisinger, and Shapiro. Using the fact that the GiveDirectly RCT didn’t target all households in a given village, and randomized the intensity of the treatment, they can estimate the subjective well-being impacts not only of one’s own wealth but also of one’s neighbors’ wealth. Their headline result is that the effect of a $100 increase in village mean wealth is a 0.1 SD decline in life satisfaction – which is four times as big as the effect of own wealth. However, that effect declines substantially over time due to hedonic adaptation. This is an important contribution in a literature that lacked credible evidence on this topic.

However, not everyone is happy that they even looked at this question. Anke Hoeffler raises a concern about the very existence of this study.

I was just overwhelmed by a sense that this type of research should not be done at all. No matter how clever the identification strategy is. Am I the only one to think that is not ethical dishing out large sums of money in small communities and observing how jealous and unhappy this makes the unlucky members of these tight knit communities? In any case, what do we learn from a study like this? The results indicate that we should not single out households and give them large sums of money. So I hope this puts an end to unethical RCTs like this one.

I think this study was fundamentally an ethical one to do, for two distinct reasons: additionality and uncertainty.

By “additionality”, I am referring to the fact that this study uses existing data from an experiment that was run for a totally different reason: to assess the effects of large cash transfers to the poor on their spending, saving, and income. No one was directly exposed to any harm for the purpose of studying this question. Indeed, these results need to be assessed in light of the massive objective benefits of these transfers. One reading of this paper is that we should be more skeptical of subjective well-being measures, since they seem to be understating the welfare benefits of this intervention.

Second, uncertainty. We had limited ex ante knowledge of what this intervention would even do. Assuming that the impacts on subjective well-being and stress could only be negative takes, I think, an excessively pessimistic view of human nature. Surely, some people are happy for their friends. The true effect is probably an average of some positives and some negatives.

Indeed, the study has results that are surprising if one assumes the stress model must hold. What we learned from this study was much more subtle and detailed than a simple summary of the results can do justice to. First off, the authors emphasize that the effects on psychological well-being, positive or negative, fade away fairly quickly (see graph below). Second, the authors can also look at changes in village-level inequality, holding own wealth and village-mean wealth constant. There the effects are zero – directly contradicting the usual statement of the stress theory. If one’s neighbors are richer, it does not matter if the money is spread evenly among them or concentrated at the top.

Figure 2 from Haushofer, Reisinger, and Shapiro (2015)
Figure 2 from Haushofer, Reisinger, and Shapiro (2015)

Third, the treatment effects are more mixed, and probably smaller, than the elasticity quoted above. There’s no ex ante reason to think life satisfaction is the most relevant outcome, and none of the other measures show statistically-significant effects. Indeed, if we take these fairly small and somewhat noisily-estimated point estimates as our best guesses at the true parameter values, we should also take seriously the effects on cortisol, a biomarker of actual changes in stress. Here, the impact is negative: an increase in village-mean wealth makes people (very slightly) less stressed. This result is even stronger when we focus just on untreated households, instead of including those who got cash transfers. One way of accounting for the variation in these estimates that improves the signal-to-noise ratio is to look at an index that combines several different outcomes. The effects on that index are still negative, but smaller compared with the direct effects of the transfer. If we look just at effects on people who did not get a transfer, that index declines by 0.01 SDs, which is only a third of the magnitude of the effect of one’s own wealth change (a 0.03 SD increase).

My conclusion from the evidence in the paper is twofold. First, there’s nothing here to suggest that the indirect effects of others’ wealth on subjective well-being are large enough to offset the  direct benefits of giving cash to the poor. Second, the evidence for direct effects of others’ wealth on subjective well-being is fairly weak. This paper is far and away the best evidence on the topic that I am aware of, but we can barely reject that the effect is zero, if at all. That casts doubt on the stress-and-inequality theory, and means that more research is certainly needed on the topic. More experiments that give money to the poor would be a great way to do that.

*As Angus Deaton explains in this fantastic JEL article, inequality has an obvious link to average health outcomes through its effect on the incomes of the poor. The stress-based theory posits that an increase in inequality would make poor people sicker even if their income remained constant.

PSA: Cut the whitespace off the edges of your PDFs to import them into TeX

These days in economics, TeX is more or less unavoidable. There’s really no better way to put equations into your documents, and it can do wonderful things with automatically numbering tables and hyperlinking to them from where they are referenced. Even if you don’t like it, your coauthors probably do. So using it is basically a must.

If you’re like me, though, you make your actual formatted tables in Excel, so you can customize them without spending hours writing and debugging code to get them to look right. This creates a problem when you want to put them into your paper: if you want to use TeX’s powerful automatic numbering features, you need to import each table as an image. You can do this using a normal picture format like PNG, but your tables will look pixelated when people zoom in. The best format to use is to import your tables as PDFs, which can scale perfectly. But PDFing your excel tables will print them to entire pages, with tons of white space. TeX will then import all the white space as well, which at best puts your table title oddly far from the content and at worst moves the table title and page number off the page.

To get around this you need to crop your PDFs from whole pages down to just the content. You can do this manually in Adobe, and I used to use a free tool amusingly titled “BRISS”. This is tedious, though, and adds another chance for human error.

Today I figured out how to use a totally automated option for PDF cropping – a Perl script called pdfcrop, which was written by Eric Doviak, an economist at CUNY Heiko Oberdiek, who is probably not an economist. Here’s how to use it in Windows. You can download the script here. Extract it and put it in the root directory of your C: drive or someplace else convenient.  pdfcrop also requires a Perl environment like Strawberry Perl (download link) and a TeX implementation like MikTeX (download link) to run. Once you get all the components installed, you will run it through the command prompt. (You can pull up the command prompt by hitting Windows+R, typing “cmd” and hitting Enter).

The command you want to run looks like this:

“C:\pdfcropscripts\pdfcrop\pdfcrop.pl” “PATH_TO_ORIGINAL” “PATH_TO_CROPPED_VERSION”

If your original tables is in “C:\Dropbox\PaperTitle\Jason’s_Awesome_Tables.pdf” then your command might look like

“C:\pdfcropscripts\pdfcrop\pdfcrop.pl” “C:\Dropbox\PaperTitle\Jason’s_Awesome_Tables.pdf” “C:\Dropbox\PaperTitle\Jason’s_Awesome_Tables_cropped.pdf”.

EDIT: This version of the command randomly stopped working for me. Here is one that I got working, that you might try if you hit the same error:

pdfcrop “C:\Dropbox\PaperTitle\Jason’s_Awesome_Tables.pdf” “C:\Dropbox\PaperTitle\Jason’s_Awesome_Tables_cropped.pdf”.

This works even on multi-page PDFs that contain many tables – it will spit out a single PDF file that has all the cropped tables in the same order. You can import the individual pages of the PDF into your TeX document using includegraphics. Doing this:


will give you just the 4th table, and you can change the page numbers to get the other ones.

Bonus font tip: if you’re making tables in Excel and want to match the default font used in TeX, it is called CMU Serif. The CMU fonts can be found on SourceForge here. Just download the fonts and drag them into Fonts window you can find under Control Panel.

EDIT: A friend pointed out that I had misattributed credit for pdfcrop – this is now fixed. It turns out there are two identically-named tools to do this. The one I linked to appears to be the better of the two since it takes off nearly 100% of the margins.

I also got some reports of errors running the command to call pdfcrop, and encountered issues myself. I have inserted an edited command that works as well (or instead, depending on your situation).

EDIT #2: When I imported this post to my new blog it dropped all the backslashes for some reason. I’ve edited the post to fix them and also correct some typos in the example commands.

Randomizing cash transfers: practical equipoise in social science experiments

When is it ethical to randomly determine the provision of a treatment to people in an experiment? Researchers designing such experiments often appeal to the principle of equipoise, which means  “that there is genuine uncertainty in the expert medical community over whether a treatment will be beneficial.” This principle captures a straightforward ethical logic: we know that ARVs are effective in treating AIDS, so it would be unethical to design an experiment that denies some AIDS patients access to ARVs. In contrast, until recently we did not know that starting ARVs immediately had health benefits for people with HIV who do know yet have AIDS. The experiment that proved that this was the case was entirely ethical to conduct.

This approach works well for medical trials, because doctors have the joint social roles of studying which treatments are effective and actually providing people with the treatments that work. Social scientists tend to be in a very different situation. First, relative to medical research, we are substantially less sure what the impacts of various interventions will be.** Second (despite what people might think about economists in particular) we just don’t have that much influence. There are many policies and programs that economists know to be effective that have little or no traction in terms of actual policies. An example that I am particularly fond of is the idea that if you want to maximize uptake and use of a product, you should give it away. The notion that people won’t “value” things they get for free is so popular that two economists actually had to go out and randomize prices for insecticide-treated bednets to prove that giving them away would work for fighting malaria. And still, I see people charging money for them.

The bednet study is a great example of what I am dubbing practical equipoise. I personally had no doubt, prior to that study, about which direction the demand curve for bednets sloped. Almost any economist would probably have felt the same way, so “clinical equipoise” did not hold. Yet policymakers felt strongly that user fees for the nets were a great thing. Practical equipoise is a situation where the science is in but policymakers don’t agree with it; while the scale of knowledge is not balanced, we can try to use persuasion and facts to balance the scale of actual practice. In this situation, randomized experiments are an ethical imperative – they benefit people who would otherwise have lost out, and also can help promote universal access to beneficial treatments in the future.

Practical equipoise holds for many policies that social scientists want to study, and particularly for cash transfers. There is a growing body of evidence that just giving money to poor people carries large benefits and few costs, leading prominent economists to advocate that evaluations of social programs should include a cash transfer arm as a basis of comparison. This is something we should probably do in general, and should definitely do as a way to evaluate giving people food handouts. Recent research by IFPRI comparing food vs. cash for helping the hungry has found that cash does much better; while their own discussion of their results has tried to take a moderate tone, the fact is that outcomes are similar for cash at a much lower cost. But people – especially the elites who make decisions about these things – remain broadly unconvinced that it is safe to give cash to poor people who need food. We are ethically obligated as scientists to push for randomized testing of cash transfers as an approach to food crises: we are highly confident they work, and need to do what we can to convince policymakers that we are right.

*Medical research is also focused on treatments that directly impact people’s well-being in an objectively-measurable way, which is relatively uncommon in social science research.

**A prominent example is the effect of moving kids from housing projects to richer ones, which was found to be surprisingly small and negative for some outcomes in analyses that focused on older children and people who volunteered to move. Recent work examining younger kids and on people who do not voluntarily sign up for housing vouchers has shown that there are in fact substantial benefits for those groups.

Unattributed quotes and the propagation of myths about homicide in America

“One study of a high-crime community in Boston found that 85% of gunshot victims came from a network of just 763 young men—or less than 2% of the local population.” So says The Economist in a review of the causes of a spike in the murder rate and potential solutions to the problem entitled “Midsummer Murder”. It’s an exciting finding – if we can identify this 2% of men and hit them with a targeted intervention, we can essentially solve America’s horrific homicide problem.

But a friend of mine pointed out an odd discrepancy within the article: it states that only 14% of murder victims are gang members. How are there all these socially-connected young men committing almost all the violence, if they are not in a gang? And it is oddly unspecific about the details of the Boston study – who are these men? Are they black, like most of the other young men discussed in the piece? To sort these things out, I googled the entire sentence to see if I could find the original study.

What I found instead was the original sentence. Papachristos and Wildeman (2014) write:

For example, a recent study of a high-crime community in Boston found that 85% of all gunshot injuries occurred entirely within a network of 763 young minority men (< 2% of the community population)

The Economist just took this sentence and did synonym replacement. Their version is quite clearly a weakly paraphrased version of the original.

Interested in the details of what was going on, I dug up the actual study being cited here, which is also by Papachristos (with Braga and Hureau).* And it turns out that the  The Economist’s quoted-without-attribution summary doesn’t even appear to be accurate. The study only looked at 763 people – not the whole community. And the 85% figure is the share of gunshot victims within the 763-person sample who are socially-connected to each other somehow. I see no mention in the article of the 2% figure that is cited by Papachristos and Wildeman (2014)  and The Economist. To be sure I didn’t overlook it, I used ctrl-F to look through the entire article for “two”, “2”, “%”, and “percent”. It appears to be a mischaracterization of the statement in the Papachristos et al. (2012) abstract that “The findings demonstrate that 85 % all of the gunshot injuries in the sample occur within a single social network”.

It might also be a true statement that is just not supported by the underlying article. Papachristos presumably has the data, and sometimes people cite their own previous papers in order to reference a dataset. Usually when you do that, you say something like “authors calculations using data from


” but maybe it got edited out.

It turns out that Papachristos and Wildeman (2014) – the other article where the unattributed quote was pulled from – actually addresses the question we are interested in: how socially-concentrated are murders. They study a poor, black neighborhood in Chicago, and find that 41% of all murders happened in a network of just 4% of the sample. The rest of the murders are actually even more spread out than you might guess – they don’t happen within the “co-offending network” – the set of people who are tied together by having been arrested together. Instead, 59% of murders are are spread throughout the 70% of the community that is not linked together by crime. While there are patches of highly-concentrated homicides the overall problem is not very concentrated at all.

That is a much less sexy finding, that lends itself much more poorly to simple solutions to problems of violence. If homicide is highly-concentrated then we can rely entirely on targeted interventions like Richmond’s program to pay high-risk men to stay out of crime – a program directly motivated by evidence that a small number of men are responsible for almost all murders.

What The Economist did here is not exactly plagiarism, but it wouldn’t fly in an undergraduate writing course either. At the same time, I can definitely empathize with the (unnamed per editorial policy) author. They might have fallen into the trap of reading the original sentence and then having trouble coming up with a truly distinct way of saying the same thing – that’s definitely happened to me before. Maybe they were worried about screwing up the meaning of the sentence by changing it too much. Or perhaps the editor cut out a citation that was in there.

Whatever the reason for the lack of attribution, it has consequences: because the quote was just lifted from another piece, the author didn’t catch the fact that it was an erroneous description of the study’s findings. If the original source of the quote had been cited, other people might have noticed that it contradicts what the quote says, or thought it was odd that they cited the source paper’s description of another study but not its own findings. Lots of people read The Economist. Policymakers thinking about how to combat homicide could be misled by this false but eye-catching statistic into investing in approaches that probably won’t work, instead of things like cognitive behavioral therapy that actually make a difference.

*I also found out that the sample in question is indeed a sample of black men – about 50% Cape Verdean and 50% African American.

Adventures in research framing and promotion

The press release headline for a new paper reads “Study: Low status men more likely to bully women online”, and the original article (ungated) is titled “Insights into Sexism: Male Status and Performance Moderates Female-Directed Hostile and Amicable Behaviour”.

What is the source of these deep insights into sexism? As SirT6 put it on r/science,

“Low status” in the context of this research means guys who are bad at Halo 3.

The headlines, and the introductory portions of both the popular and academic versions of the article, state findings that are much more forceful and general than the actual article. (Incidentally the press release is also by the original authors, so they are responsible for what it says.) The core finding of the study is that the number of positive comments made by male players towards female players goes up as the male players skill rises. They find nothing for negative comments. It’s pretty hard to sell.

I find the paper itself pretty interesting, and I do think the results fit the authors’ hypotheses. I do take issue with their inclusion of players’ in-game kills and deaths as predictors in their regression: those are outcome variables, and putting them in your regression on the right-hand side will lead to biased coefficient estimates. I also think the graphs overstate their findings and should show the binned values of the actual datapoints, and the confidence intervals for their fitted curves. But it’s a nice contribution in a clever setting and it has value.

What I see as a much bigger problem with the paper is how the research is being pitched, and it’s really not the authors’ fault at all. A lot of media attention goes toward the systematic biases in scientific research due to publication bias and selective data analysis choices, but there is a huge elephant in the room: framing and salesmanship. The success of a paper often depends more on how the authors frame it (relative to the audience of the journal, their specific referees, and the wider public) than on the fundamental scientific value of the work. In part, this is another way of saying that successful scientists need to be good writers.

But it also means that there is an incentive to oversell one’s work. I see this quite a bit in economics, where papers that are fairly limited in their implications are spun in a way that suggests they are incredibly general. All the incentives point in this direction: it’s hard to make it into a top general-interest journal without claiming to say something that is generally interesting.

The spin here is particularly strong: the paper that shows that having a female teammate causes male Halo 3 players to make more positive comments if they are high-skilled and fewer if they are low skilled, and got sold as saying that males online in general engage in more bullying if they are low-status. It’s often more subtle, leaving even relatively knowledgeable readers clueless about the limitations of a work, and leading to conclusions about a topic that are unsupported by actual evidence.