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Freaks and Geeks

by Noam Scheiber
Post date: 03.21.07 — Issue date: 04.02.07

One of the few papers I actually read as a grad student was written by
a pair of economists named Josh Angrist and Alan Krueger. In the early
’90s, Angrist and Krueger set off to resolve a question that had been
gnawing at economists for decades: Does going to school increase your
future wages? Intuitively, it seemed obvious that it did. When you
compared the salaries of, say, Ph.D.s with those of high-school
dropouts, the grad-school set almost always did better. The question was
whether education accounted for the difference. What if it was simply
the case that smarter people spent more time in school and that their
bigger salaries reflected intelligence, not education? One couldn’t be
sure. The only way to get to the bottom of it would be a ghastly social
experiment, wherein you took a group of students and randomly sent half
to the local vo-tech institute while forcing the other half to study
feminist literary theory. Even an economist wouldn’t be so audacious.

That’s where Angrist and Krueger came in. In the paper, they pointed out
that two features of the public school system allowed you to answer the
question without all the uproar. First, most states force students to
attend school until age 16. Second, for many decades, students started
school the year they turned six. The upshot was that, if I were born in
January and you were born in December of the same year, and we both
dropped out at 16, then the rules forced you to stay in school almost
one year longer. (We’d start school the same year, but I’d turn 16
midway through tenth grade and you’d hit 16 midway through eleventh.)
The additional schooling foisted upon one group by this arbitrary state
of affairs produced a scaled-down version of our experiment, allowing
Angrist and Krueger to conclude that education did, in fact, help people
earn more money.

I probably first came across this paper in 1999. At the time, it struck
me as a neat trick, certainly a welcome diversion from the stultifying
technical literature economists must imbibe, but largely unremarkable
beyond that. Three years later, having escaped the academic track, I was
nonetheless spending a lot of time in Cambridge, Massachusetts, where I
moonlighted as an economics poseur and consorted with the smartest young
economists in the world. And one of the things I was shocked to learn
was that Harvard grad students had invested the Angrist and Krueger
paper with totemic significance.

It quickly became apparent that the way to win acclaim as a grad student
was to devise a similarly ingenious method of tackling a problem.
Several years after his paper on schooling, Angrist noticed that the
Armed Forces Qualifying Test had been misgraded for a few years in the
late ’70s. This had opened the doors to thousands of subpar applicants
and allowed Angrist to compare the lucky underachievers with the people
rejected once the glitch got corrected, thereby isolating the impact of
military service on wages. The practical effect was to send the grad
students scrambling to find other instances in which life-altering
decisions had been handed down incorrectly. In 2000, a Harvard professor
named Caroline Hoxby discovered that streams had often formed boundaries
to nineteenth-century school districts, so that cities with more streams
historically had more school districts, even if some districts had later
merged. The discovery allowed Hoxby to show that competition between
districts improved schools. It also prompted the Harvard students to
wrack their brains for more ways in which arbitrary boundaries had
placed similar people in different circumstances.

Every few weeks, when a student would stumble onto some new test-grading
error or fatefully drawn boundary–what economists call
“instruments”–word of the discovery would rocket through the
department. The discoverer would become instantly, if momentarily,
famous, like the holder of a winning card at a Bingo hall, and inspiring
the same mix of reverence and jealousy. A typical conversation around
the snack machine at the National Bureau of Economic Research, where
many Harvard students had cubicles, went something like: /Hey, did you
hear that so-and-so found this crazy example of excess tax refunds in
western Manitoba in the early ’60s?/ At which point the other would
reply, /Uh, no, wow, that’s, uh, great/, and then scamper back to his
desk to brainstorm for some similar quirk of public policy. At an age
when most people brood that life is too random and arbitrary, these
people’s biggest complaint was that it wasn’t random and arbitrary
enough.

In retrospect, I have come to see this as the moment I realized
economics had a cleverness problem. How was it that these students, who
had arrived at the country’s premier economics department intending to
solve the world’s most intractable problems–poverty, inequality,
unemployment–had ended up facing off in what sometimes felt like an
academic parlor game?

With the 2005 publication of /Freakonomics/, the breezy exposition of
Chicago economist Steven D. Levitt’s oeuvre, the rest of the world has
come to see that economists are capable of spectacular feats of
cleverness–and to a degree I couldn’t imagine back in my poseur days.
In the search for what’s known as “clean identification”–a situation in
which it’s easy to discern the causal forces in play–Levitt has turned
to such offbeat contexts as Japanese sumo-wrestling and the seedy world
of Chicago real estate. He has studied racial discrimination on “Weakest
Link,” a once-popular game show, and reflected on the scourge of
white-collar bagel-filching. This has, in turn, inspired a flurry of
imitators, including papers on such topics as point-shaving in college
basketball, underused gym memberships, and the parking tickets of U.N.
diplomats.

Within the frequently tedious body of economics scholarship, these
papers stand out as fantastically entertaining. Judging from the
dizzying sales of /Freakonomics/ and the thousands of lecture halls
across the country now bursting with econ majors, they’ve also been
wildly successful at ginning up interest in the discipline. But it does
make you worry: What if, somewhere along the road from Angrist to Levitt
to Levitt’s growing list of imitators, all the cleverness has crowded
out some of the truly deep questions we rely on economists to answer?

It would be wrong to pretend that this cleverness problem only dates
back a decade or two. Academic economics has sometimes valued ingenuity
above usefulness since at least the Second World War. In 1996, days
after winning the Nobel Prize in part for a theoretical model he’d
pioneered in the ’60s, Columbia economist William Vickrey confessed that
the paper’s practical contribution was next to nil. “At best, it’s of
minor significance in terms of human welfare,” he told /The New York
Times/.

Still, for more than a generation, it was mostly theorists like Vickrey
who had a monopoly on cleverness. The early postwar empiricists–that
is, the people who dealt with real-world data–were, for the most part,
earnest, stubborn men. They tackled the era’s thorniest questions with a
freakish determination. Harvard economist Zvi Griliches devoted decades
to the problem of productivity growth, the chief determinant of rising
living standards. His colleague Simon Kuznets spent half his career
devising the measure of economic growth we still use today. If these men
sometimes gave the impression that economics was a life-and-death
proposition, well, that was no accident. /Life/ to them was a
life-and-death proposition. Griliches had survived the Holocaust.
Kuznets had endured the German occupation of his native Ukraine.

By the ’80s, however, the data-crunchers had come down with a crisis of
confidence. In one famous episode, the eminent economist H. Gregg Lewis
reviewed several studies on unions. What he found was alarming: Some
papers reported that unions strongly increased wages; others reported
exactly the opposite. The difference, in most cases, was simply the
assumptions the authors had made.

Critiques like this tipped the discipline into a prolonged bout of
soul-searching. The old approach had been sweeping in its ambition. But
what good were ambitious goals if the best you could do was “on the one
hand/on the other hand”style equivocation or, worse, plain gibberish?
“People didn’t believe the estimates being produced,” recalls David
Card, then a rising star at Princeton. “They felt the evidence in
economics was not very credible.” Economists had long aspired to
science. Suddenly they faced a harrowing thought: What if they were no
better at pinning down truth than the average critical studies major?

Having glimpsed this nihilistic vision, many economists ran screaming in
the opposite direction. They concluded that the path to knowledge lay in
solid answers to modest questions. Henceforth, the emphasis would be on
“clean identification,” on sorting out what caused what.

The early practitioners of this approach–Angrist, Krueger, Card–had
well-earned reputations as crafty researchers. But, by and large, all
three men used their creativity to chip away at important questions. It
was only in the late ’90s that the signs of overreach became apparent.
To some professors at top departments, clean identification became a
fetish. “Almost every student, myself included, had the terrible
experience of getting up in front of the [professors] for whom
identification is the Holy Grail, and getting cut to shreds when your
identification strategy doesn’t pass muster,” recalls a recent Harvard
Ph.D. The problem is that there are only so many big questions that
misgraded tests or arbitrary boundaries can shed light on. If you’re
wedded to these techniques, eventually they lead you in obscure
directions. “People think about the question less than the method,” says
Berkeley professor Raj Chetty, one of the most sought-after Harvard
graduates in recent years (and a notable exception to this trend).
“They’re not thinking: What important question should I answer?’ So you
get weird papers, like sanitation facilities in Native American
reservations.”

Many young economists began shunning big questions altogether. Jim
Heckman, a Nobel Prizewinning labor economist at the University of
Chicago, illustrates the point with a story. A few years ago, he struck
up a conversation with a promising assistant professor. Before long,
Heckman began to gripe that economists lacked a comprehensive measure of
all the obstacles a child might face in life–education, nutrition,
family environment, and so on. There was no way to tell if childhood
disadvantages were getting better or worse.

He encouraged the young economist to produce such a measure. “You’re
absolutely right. It’s paramount, of first-order importance,” the woman
replied. But there was zero chance she’d pursue it. “It would take years
to do,” she explained apologetically. The woman had clearly made the
right career decision: No one coming up for tenure could afford that
kind of time while her colleagues published a stream of small-bore
papers. On the other hand, says Heckman, “How long did it take Madame
Curie to purify radium? Two or three years? If she was somehow told,
like the grad students in our program, If you can’t solve the problem in
a week or a month, drop it,’ a lot of big problems would have been
dropped.”

Heckman’s allusion to a certain pedagogical technique is almost surely
a shot at his Chicago colleague, Steve Levitt. Levitt has been known to
discourage students from laboring too long on a question for which the
data are unlikely to produce a useful result. “I’ve always been someone
who’s thought it’s better to answer a small question well than to fail
to answer a big question,” he says. This much should not be surprising.
Levitt is the product of the same environment that birthed the
clean-identification movement.

After graduating from Harvard and doing a brief stint in management
consulting, Levitt earned a Ph.D. from MIT in 1994, completing the
program in a mere three years. “In the early ’90s, if you had a really
great natural experiment, as we called it, you’d get yourself a job,” he
says. Levitt, it turned out, had many. While still a student, Levitt
wondered whether money drives election results or if the better
candidate simply raises more money. He ingeniously demonstrated the
latter and published the results in a top journal. Another early paper
found that a slight increase in the chance of arrest dramatically
deterred auto theft. Levitt discerned this by studying cities that had
approved the use of Lojack, a transmitter that leads police to stolen
cars. In 2001, Levitt published what is probably his most controversial
finding to date: a paper highlighting the connection between the
legalization of abortion in the ’70s and the falling crime rates of the
’90s. Levitt argued that unwanted children are most at risk of becoming
criminals. Abortion, he concluded, lowered crime rates by reducing
unwanted pregnancies.

Some of these papers made genuinely important contributions. The Lojack
paper helped demonstrate that theft is a fundamentally rational
phenomenon and can therefore be discouraged. This insight alone might
have justified Levitt’s John Bates Clark Medal, a prize awarded every
two years to the most outstanding economist under 40. But, at times,
Levitt gave the impression he was more interested in clever techniques
than answers to questions. In a 1997 paper, for example, Levitt argued
that hiring more police decreases crime, a proposition for which there
was surprisingly little evidence. (The fact that municipalities expand
police departments when crime rates rise tends to muddle the picture.)
To prove it, Levitt needed to simulate an experiment in which the size
of a police force was randomly increased. His solution was to exploit
the fact that mayors often hire more police officers in the run-up to an
election. The only hitch, as a grad student later pointed out, was that
mayors up for reelection don’t actually hire many police officers, at
least not enough to show that they lower crime.

Whatever the flaws in this study, they were clearly the product of too
much ambition, not too little. A few years later, however, Levitt
debuted a new kind of paper: an investigation into offbeat phenomena
from daily life. One of the earliest examples pondered the strategies
soccer players employ when taking penalty kicks. Another paper studied
corruption in sumo-wrestling tournaments as a window onto the power of
incentives. Not long after, Levitt conducted an exhaustive inquiry into
“Weakest Link,” a game show in which contestants voted to remove a
player after each round of trivia questions. Tallying the voting data
revealed that contestants were discriminating against Latinos and the
elderly but not blacks and women.

In some respects, the papers were just an extreme version of the Harvard
approach–an attempt to shrink a question down to the point that you can
answer it. Except that, in Levitt’s case, the question hadn’t just
shrunk. It had traveled several hundred miles from its original starting
point. Take the “Weakest Link” paper: While the game show did provide a
pure setting for observing discrimination, there was no reason to think
we could extrapolate from “Weakest Link” contestants to, say, hiring and
promotion decisions, where discrimination often intersects with
economics. Set aside the fact that the logic governing “Weakest Link”
votes may be completely different than the logic that reigns in the
typical HR department. The bigger problem is that most hiring and
promotion decisions don’t take place in a Hollywood studio before a
national TV audience.

Levitt is charmingly, almost painfully, self-effacing when you mention
these reservations. “There’s no question I have written some ridiculous
papers,” he says. By way of explanation, he draws an analogy to the
fashion industry: haute couture versus pr?t-?-porter. “Sometimes you
write papers and they’re less about the actual result, more about your
vision of how you think the profession should be. And so I think some of
my most ridiculous papers actually fall in the high-fashion category.”

Predictably, not every economist buys this rationale. Not even every
economist at Chicago, where Levitt’s influence over grad students (whom
he attracts), young faculty (whom he helps recruit), and the prestigious
/Journal of Political Economy/ (which he co-edits) have aroused the ire
of an older generation of researcher.

Easily the most famous of the dissidents is Heckman. If Levitt is known
for his novelty, the hallmark of Heckman’s work on such issues as
education and job training is its painstaking attention to detail. A few
years ago, Heckman was rumored to be so upset over the direction of his
department that he began looking to leave. Chicago had never been an
ideal place to do empirical work. Nobel Prizewinning theorists like Gary
Becker and Robert Lucas disliked dirtying their hands with data. Now the
department was finally warming up to data-crunchers … and they were
the kind Heckman deemed useless. “Chicago has been a little
disappointing in that it hasn’t been more firm in rejecting cute and
clever,” he laments.

Not that Heckman has been shocked by the development. It is sometimes
said that healthy departments have a straightforward division of labor:
The theorists generate predictions, and their colleagues test them with
data. Alas, this process can be a drag for the people being scrutinized.
It’s much more fun to generate pie-in-the-sky predictions when you don’t
have some killjoy looking over your shoulder. Which is why, from the
perspective of the theorists, the ideal colleague may be someone less
fastidious. Someone who studies the offbeat and clever, not the
discipline’s central questions. Someone who, you might say, looks less
like Jim Heckman and more like Steve Levitt. “Rigorous theory and
bullshit empirical work can co-exist,” Heckman sighs. “It leaves the
rigorous theorists to make up the numbers they want.”

Each year, the Harvard economics department invites a handful of
eminent scholars to participate in its Political Economy Lecture Series.
Standard operating procedure is for the speaker to discuss some new
paper or avenue of research. Previous speakers have held forth on such
eye-glazing subjects as “Rule Rationality versus Act Rationality” or
“Equilibrium Contracts for the European Central Banker.” In the spring
of 2002, Harvard landed Levitt.

Levitt doesn’t immediately strike you as a mesmerizing speaker. His
voice is too high, except when it’s trailing off at the end of a
sentence. He leans heavily on the word “OK.” He is lanky and
concave-chested and often fails to make eye contact. But Levitt has a
droll magnetism, a certain anti-charisma. Combined with his eclectic
interests, it made the Harvard talk a hit.

Levitt framed his discussion as a how-to guide for practicing oddball
economics. “He talked about his kick-ass creative papers, kind of a
prelude to /Freakonomics/,” recalls one person in attendance. “Here are
the lessons you can draw to improve your own research, how you can do
clever, appealing papers yourself.” As he was wrapping up, Levitt
reflected on the choices facing grad students: /If you think you can do
as well in traditional topics as someone like Marty Feldstein/–a giant
of the profession–/you should pursue that/, he said, at which point
knowing laughter broke out. /But/, he continued, /if you don’t feel like
you’re up to that, you might want to think about alternative topics/.
The message resonated loudly. One student watched classmates spend the
next several weeks on high alert for some curiosity of daily life around
which they could build a paper.

If Levitt were literally holed away in some ivory tower, emerging only
every so often to distract economists from their thoughts about growth
and inequality with another clever curiosity, he would undoubtedly be a
force for good in the profession. It is not exactly earth-shattering to
learn that sumo wrestlers respond to incentives like the rest of us or
that soccer players behave strategically. But it’s not completely
trivial, either. The occasional confirmation of economic theory in
contexts people can relate to may even act as a check against excess in
the other direction–against useless esoterica. It would be far more
disturbing if we /never/ observed such behavior in these settings.

But if one Levitt is desirable, two may be pushing it, and more than
that might be a problem. Which makes it somewhat alarming that, between
his academic success, his popular acclaim, and his personal charm,
Levitt may be shaping a generation of young economists.

One growth industry in recent years has been what you might call the
lookie-here paper: a small-scale setting for observing some broad
principle of economics. Many of these papers deal with sexy topics like
corruption and, well, sex. One top journal recently published a paper
deducing that Iraq had received billions in kickbacks from rogue buyers
under the Oil-For-Food program. Another recent paper, this one in the
/Journal of Political Economy/, demonstrated that johns in Mexico pay
prostitutes more for unprotected sex than sex with a condom. Both of
these findings may be of journalistic interest. But the fact that Saddam
Hussein would try to profit from a scarce commodity, or that people
might pay extra for services they value more, will surprise no one who
has opened an economics textbook lately.

A companion class of papers boast similar ambitions, but with one small
difference: Instead of demonstrating all the offbeat places in which the
standard economic model applies, they demonstrate where it breaks down.
The first generation of so-called behavioral papers vastly enriched our
understanding of how real human beings make decisions, as opposed to the
constantly maximizing automatons of economic theory. Economists William
Samuelson and Richard Zeckhauser famously observed that people have a
huge bias in favor of the status quo, which sheds light on why, for
example, they fail to enroll in 401(k)s.

But subsequent generations of behavioral work have increasingly focused
on the picayune. One recent paper in a top journal, /The American
Economic Review/ (/AER/), documented how people pay hundreds of dollars
to belong to gyms they visit infrequently. A forthcoming /AER/ paper
finds that catalog shoppers overindulge in cold-weather clothing when
the temperature abruptly drops. These papers invariably predict that
such irrationality will recur in more meaningful contexts–for example,
in decisions about jobs or home purchases. Maybe. On the other hand,
maybe the only reason people behave irrationally when buying snow boots
is that /no one gives a damn about snow boots/. At least not the way
they give a damn about their jobs and houses.

Unquestionably, much of what’s driving this descent into “cute-o-nomics”
is the burst of media attention now devoted to economics papers. “It’s
very clear that the incentives are to try to do work that gets some
public attention. To some extent, that work gets accepted in top
journals. You can’t blame kids for doing it. I wouldn’t blame Levitt,”
says David Card, now of Berkeley. But people like Card sometimes worry
about the consequences. “It is exactly like postmodernism in the
humanities,” he groans. “What is there to say about Beethoven anymore?
… Every moron can’t understand technical orchestration, doesn’t know
the history of music. So you write about him having a gay affair with
his nephew.”

Sadly, Card isn’t far off. A few years ago, Levitt supervised a Ph.D.
student named Andrew Francis, who now teaches at Emory University. The
paper Francis took with him into the job market was called “The
Economics of Sexuality: The Effect of HIV/aids on Homosexual Behavior,
Desire, and Identity in the United States.” In it, Francis attempted to
demonstrate that certain homosexual men become heterosexual when aids is
widespread. Granted, there is a legitimate, if sometimes tawdry,
literature examining the way sexual behavior responds to disease. But
Francis wasn’t talking about changes in behavior–less promiscuity,
greater condom use, etc. He was talking about changes in /sexual
orientation/.

This last may look like a different trend than the bull market in
lookie-here papers–more economic imperialism than Harvard-style
empiricism. It’s not so much that Francis had dreamed up a clever
context in which to get at a mainstream question. It’s that he’d brought
economics to bear on a distinctly non-economic phenomenon, one far more
likely to be governed by the forces of biology and psychology than
supply and demand. But, in a way, this style of research has also been
enabled by the techniques practiced in Cambridge and refined by Levitt.
The new imperialists have vast confidence in their ability to extract
causality from data. This confidence has, in turn, sometimes led them
into territory best left to other disciplines.

Perhaps the most infamous example is a paper written by a recent Harvard
Ph.D. named Emily Oster. While still an undergraduate, Oster had become
fascinated by the so-called “missing women” problem–the hypothesis,
attributed to Amartya Sen, that gender discrimination in Asia has
created a vast shortage of women. In some cases parents abort daughters,
in some cases they commit infanticide, in some cases they simply don’t
care for their daughters as diligently as they should. Whatever the
cause, Sen has suggested there could be as many as 100 million “missing
women” in countries like China, India, and Pakistan.

Years later, while wrapping up her Ph.D., Oster stumbled onto a
seemingly unrelated fact: a small medical literature suggesting that
women with hepatitis B were far more likely to give birth to boys. What
followed was a series of sophisticated natural experiments, the upshot
of which was to demonstrate that 100 million women hadn’t gone missing
after all. Instead, unusually high rates of hepatitis B had arranged it
so that Asian mothers were producing far more boys than nature’s track
record would suggest.

It was a fabulously compelling result, one that partially absolved whole
societies of lurid crimes against their children. It was also a
vindication of the /Freakonomics/ worldview. Levitt published Oster’s
paper in the /Journal of Political Economy/. He and his /Freakonomics/
co-author, Stephen Dubner, took to the pages of /Slate/ to breathlessly
retell her “economics detective story.” And then, just as suddenly, it
all fell apart. A snot-nosed grad student from Berkeley pointed out that
hepatitis B couldn’t possibly explain the missing women problem. It
turned out Asian women gave birth to daughters at the same rate as women
everywhere else, at least during their first pregnancy. It was only
during subsequent births that the ratios changed. Either a bunch of
Asian women were running out to get hepatitis B in between their first
and second pregnancies, or, as Sen feared, people were taking dramatic
steps to avoid ending up with two girls.

In a sense, the split between people like Jim Heckman and Steve Levitt
is a split between the nerds and the clevers. The nerds complain that
Levitt and his ilk are so far removed from using meat-and-potatoes
economic theory they may as well be practicing journalism. “In some
quarters of our profession, the level of discussion has sunk to the
level of a /New Yorker/ article,” Heckman griped in a 2005 interview
with the Minneapolis Fed. “The authors of these papers are usually
unclear about the economic questions they address.”

The clevers deny that their research turns its back on economic theory.
They complain that the nerds insist upon a kind of sadomasochism that
does little to advance the cause of knowledge but makes them feel like
they’re doing God’s work. “The structural Gestapo out there acts as if
it can’t be useful if it’s not hard or complicated. We should have a
middle ground,” Levitt told me.

All of which may just be garden-variety academic squabbling, except that
Heckman does raise a valid point. One of the statements Levitt has
become famous for since /Freakonomics/ is his observation that
“economics is a science with excellent tools for gaining answers but a
serious shortage of interesting questions.” What is one to make of a
discipline that heaps scorn on its own raison d’?tre?

This question turns out to be particularly poignant for someone like me.
As a grad student, I was constantly torn between my own prurient
interests and the belief that real economists tackle noble but boring
subjects. My first shot at a thesis topic was a model of something I
pompously dubbed “extended adolescence”: basically, how it is that
certain members of my generation get to piss away their twenties before
settling on a career. (And, more to the point, why this slacker behavior
should be subsidized.) When that didn’t pan out, I drifted to a slightly
more conventional but still narrow question about whether prison labor
leads to higher wages once convicts rejoin society.

Finally, with time running out and no luck pinning down data, I settled
on a genuinely important topic: how new technologies displace old
technologies, using mass transit as a case study. I somehow convinced a
man named Paul David to supervise the project. David, in addition to
showering me with the patience and generosity of a parent, was arguably
the world’s foremost expert on technology adoption. Our collaboration
taught me what it means to do serious, careful research.

It also happened to be one of the most tedious experiences of my life.
So tedious, in fact, that previously tedious exercises–like reading
scholarly works of history or /The New York Review of Books/–suddenly
seemed like pleasant diversions. Increasingly, I felt oppressed by the
prospect of spending years on some intractable problem. I chafed at the
obligation to do “socially useful” work. I wanted the freedom to pursue
whatever seemed interesting and to drop whatever didn’t. Journalism, it
turned out, was /precisely/ what I wanted to practice. Maybe then I
could tap my economics training in the highly seductive manner of a
Malcolm Gladwell or a Michael Lewis, not wear it around like a hair
shirt. How ironic, then, that academic economics was making room for us
lightweights at the very moment I decamped for journalism. How scary.

When I raise this issue with Levitt, he is almost apologetic: “There
needs to be a core for work on the periphery to make any sense. I don’t
think we would want to have a whole profession with dilettantes like me
out doing what I do.” But, in nearly the same breath, he adds: “The
simple fact is that it’s hard to do good research. … To the extent
that you can do interesting research that teaches us something about the
world, and entertains along the way, that’s not so bad.”

Noam Scheiber is a senior editor at The New Republic.