Did the iPhone Cause the Baby Bust?
I'm not so convinced. An interesting new paper highlights the power and pitfalls of simple stories
A new NBER working paper (not yet peer-reviewed) was published this week with the catchy title “Is the iPhone Birth Control?” The paper concluded that 33-52% of the decline in US birth rates from 2007-2011 was explained by the introduction of the iPhone.
Naturally, this finding was born to make headlines. My favorite so far:
But like many headline-friendly studies, it’s worth looking under the hood before pressing the “I believe” button.
Extraordinary claims require extraordinary evidence
First, the good news. The authors undertake careful empirical work that tackles a BIG societal question—why have US birth rates fallen so much since 2007?
Notice I said “question” rather than “problem”—major demographic changes almost always have important implications, but that doesn’t mean they are a “crisis.” Teen pregnancy rates (which used to be considered their own “crisis”) have gone down a lot over this period. Read more about recent US fertility trends here:
Despite the overconfident claims of many a podcast bro, big shifts in population trends like birth rates (or life expectancy) usually defy simple explanation. For example we still don’t really know what caused the Baby Boom, which was a big deviation from previous trends towards lower birth rates in the US and around the world.
As with death rates, hundreds of factors may affect a population’s birth rate at any moment, and it’s the combination of these that produce a trend. So, we should approach with healthy skepticism any findings that claim to explain a substantial portion of a trend in one fell swoop… or with one single electronic device.
Smartphones and algorithmic social media have undoubtedly changed our social worlds forever. We all recognize this in our own lives. Like many new technologies before them, they are blamed for a range of societal ills from the youth mental health crisis to increased political polarization. But even for narratives that ring true, it’s hard to prove cause and effect at the population level, because human behavior is complex, and lots of trends move at the same time, for example:
(Check out Tyler Vigen’s site for more fun spurious time trends.)
Social scientists can’t manipulate their “treatments” experimentally like lab or clinical scientists can. Much of our understanding of past demographic trends comes not from natural experiments but from rich description layered with different types of evidence to paint a plausible picture of might have happened. Even then, we can still debate whether such accounts fit the data, but the triangulation approach acknowledges the complexity of explaining population change. Ming Yang’s recent post on the Great Fire of London not ending the plague resonated as a broader example of the appeal of simple narratives throughout history.
Today’s social scientists (especially economists) tend to prize clean causal “identification” through “natural” experiments, with less emphasis on building big-picture narratives with theory and rich description. I came of age right in the thick of this “credibility revolution” as a grad student at Princeton, so I relate to that rush of excitement at the prospect of discovering a clever natural experiment. But I’ve also been around long enough to see how the quest for clever identification can sometimes lead us to miss the forest for the trees.
There is nothing “natural” about this experiment
The new paper takes advantage of a feature of the early US iPhone roll-out—service was available through only one cellular carrier (AT&T) from June 2007 through February 2011. AT&T coverage varied geographically, meaning not everyone could really have an iPhone in those early years (unless they wanted a very expensive iPod in their pocket). The authors use variation in AT&T’s 3G coverage across US counties as a proxy for early iPhone exposure, comparing fertility rates in counties with near-universal coverage to counties with almost none from 2008-2011.
Despite the exclusivity of early iPhone access, this design cannot be called a “natural experiment.” Geographical AT&T 3G coverage was not random, or even “quasi-random” (see map above). Companies do their best to make money (!), and so infrastructure investments by AT&T track closely with county characteristics such as higher population density and higher household incomes. Ideal natural experiments start from the premise that the experimental “treatment”, in this case AT&T 3G coverage, can be considered as good as random because of some quirk of policy or nature. Think about the design of the recent shingles vaccine and dementia papers—people born on either side of a birthday cut-off for vaccine eligibility should be very similar to one another. But if vaccine eligibility had been determined instead by geography—say everyone in London got it first—the roll-out would not have been a “natural experiment” with a clean treatment and control group. Of course even the best “natural experiments” are not perfect, so such papers usually spend a lot time persuading the reader why the exposure really does mimic an experiment.
I’ve seen the authors refer to this paper as a “natural experiment” on-line, but the paper does not spend any time making the argument that geographic variation in AT&T coverage is quasi-random, or describe what historical, economic, or geographic factors contributed to the observed variation in their key exposure.
The non-randomness of the AT&T exposure is confirmed in the paper’s Table 1, which shows big differences in treated and control counties. Low AT&T coverage counties have less of their population classified as urban than treated counties, (28.2% compared to 66.4%) and much lower median household income ($56,300 vs $74,000). These are huge differences in key demographic variables, and certainly means that these counties also differ in hundreds of ways that are not reflected in this table.
The authors do their best to make this non-random AT&T exposure more like a real experiment, as should be the goal of any observational study. They use two different statistical approaches to narrow their comparison to counties that are most similar to one another except for their AT&T coverage. But this is easier said than done.
Because this is a long, detailed paper, I’ll summarize my main takeaways more concisely first, but I include a deeper dive at the end of this post for those interested in more methodological detail.
Apple (s) and Oranges, Re-weighted.
To repeat: High AT&T coverage was not random. While it’s a neat idea to think about AT&T coverage as a proxy for early iPhone use, as we’ve seen, “treated” counties with >90% AT&T coverage were significantly more urban and affluent than counties with <10% coverage. For me, this is a potentially insurmountable issue that makes the bar incredibly high for me to believe these estimates are picking up an effect of the iPhone vs lots of other things correlated with economic geography. The statistical methods used to make high- and low-AT&T-coverage counties as comparable as possible are reasonable choices given the data, but they aren’t magic. The difference-in-difference model assumes that birth rate trends in the treated and control counties were moving in tandem (“parallel trends”) before the introduction of the iPhone. The paper imposes these parallel trends statistically, but gives us very little detail on which counties end up being good controls. The pre-iPhone period used for estimation was quite short (2003-2007), a serious concern for a method whose validity rests on the assumption of creating comparability of pre-intervention trends.
While the authors do a bunch of checks of their models, none of them address the biggest threat to validity of the analysis, which is the assumption that post-period trends would not have diverged for any other reason.
If birth rates in wealthy, urban counties would have fallen more than in rural counties from 2008 regardless (for example, if the recession hit them differently), this would show up as an iPhone effect, despite our best econometric gymnastics.
(Head to the bottom for more analysis red flags that stuck out to me).
Reality check: Early iPhones couldn’t do much. And not many people had them.
The next big stumbling block for me is the real-world plausibility of these estimates. The headlines ring true because we are thinking about how smartphones pervade very aspect of our lives today, from Uber to food delivery to dating apps to TikTok to group chat notifications and so much more. But those significant lifestyle changes took many years to play out, while this study is focused tightly on the period 2008-2011, when much of this ecosystem did not exist yet.
So if you do believe the strong assumptions built into these statistical models, you still have to contend with the estimated effect sizes, which are large. Recall the authors state that 33-52% of the decline in US birth rates from 2007-2011 is attributable just to the iPhone. Is such a rapid, dramatic effect of a new product on the market plausible? This isn’t like flipping a switch, the technology needs time to be disseminated widely and then work through social and behavioral mechanisms.
The authors propose (but do not test) that the iPhone reduced birth rates by:
displacing in-person socializing that leads to sex
increasing pornography consumption as a substitute for partnered sex
increasing access to information on contraception and abortion.
While much of this makes sense, it’s most plausible as a post-2011 story. Many of us lived through this, but a reminder of the rough timeline:
June 2007: iPhone launches, costing $499 plus a $59.99/month two-year contract. Built-in Apps included: Messages, Calendar, Photos, Camera, YouTube, Stocks, Maps, Weather, Clock, Calculator, Notes, Phone, Mail, Safari, and iPod. No Third Party Apps or App Store. The original “Edge” network was VERY slow, not suitable for streaming video.
July 2008: The App Store launches, 3G rolling out, but speeds were still slow and variable, not great for video. Among the top apps were “Koi Pond” and “Texas Hold ‘em.”
October 2010: Instagram launches, four months before the study window closes.
July 2011: Snapchat launches, after the study period ends.
These were not the all immersive, constant notifications smartphones of today. What’s more, rates of iPhone ownership in this period were low. The authors cite data showing that only 12–13% of US adults aged 20–24 owned an iPhone in 2011, which was at the very end of the study period. Presumably the average over the whole study period would be considerably lower, especially for teens.
Between rudimentary capabilities and low rates of ownership, it is difficult (for me) to believe the early iPhone rollout could generate such detectable changes in behavior and fertility from 2008-2011. And this is the key point-- the critique is not that smartphones or the internet have had no impact on socializing, relationships, or birth rates in the last twenty years. But this paper makes a very specific claim, that they have identified a large causal effect on fertility of the iPhone introduction specifically from 2008-2011, net of broader trends in internet use.
Overall, the large effect sizes themselves are a red flag to me, suggesting that high AT&T coverage is serving as a proxy for broader economic & geographic dynamics correlated with fertility.
The Elephant in the Room: The 2008 Recession
Besides the iPhone, what else was happening from 2008-2011? The Great Recession, officially running from December 2007 to June 2009, was the longest and most severe period of economic contraction in the United States since World War II. Such a large economic shock impacts everyone, but the effects still vary a lot, especially by geography. The housing crisis hit urban areas particularly hard, precisely those counties “treated” with high AT&T coverage. The county-level fixed effects and other statistical controls the authors employ can’t account for the main potential problem here—that the impact of the Great Recession was different in richer, more urban counties—the same ones with high AT&T coverage.
A large existing literature has examined at the impact of the Great Recession on fertility in the US. For example Schneider (2015) found that fertility fell the most through 2011 in states that experienced the highest levels of foreclosure and unemployment. Wu and colleagues have a brand new paper in the journal Demography estimating impacts of the Great Recession for US women of different birth cohorts. Of course these papers face similar challenges with causal identification, but the patterns they identify are highly relevant to the validity of the research design of iPhone paper, so it would be nice to see the authors engage with the existing recession and fertility literature directly.
The authors do a lot of due diligence to try to account for this fundamental lack of comparability across treatment and control counties, including economic changes that might have happened during the Great Recession. This is very welcomed, but taken as a whole, it didn’t do a lot to convince me that the estimates could be interpreted as a causal iPhone effect.
(I dig into the “placebo” tests more below, but the most convincing test for me would be to check whether the % AT&T coverage variable also predicts different county-level economic outcomes, such as housing foreclosures. If it does, this confirms a likely Great Recession effect. If it doesn’t, the proposed effect on fertility would more believable.)
Smartphones: Confirmation, or Confirmation Bias?
Overall, my biggest concern with the paper is the strength of the claims in the conclusion and abstract. “Overall, the diffusion of the iPhone explains 33-52% of the decline in the general fertility rate among women aged 15-44.”
Not only does this statement take the causal estimates as true, it requires scaling up the estimated treatment effects to the whole population. The authors do this by taking the “iPhone effect” size, scaling it by each county’s AT&T coverage share, and calculating a counterfactual birth rate in the absence of the iPhone. This may be a reasonable way to contextualize their statistical estimates, but it doesn’t come without assumptions. For example, such scaling assumes the “iPhone effect” is linear in AT&T coverage share, which doesn’t fit well with the idea that there would be social spillovers when a higher proportion of people are using the technology. The abstract also isn’t clear that this refers to the 2007-2011 period, with the opening sentence referring to the fall in US fertility from 2007 to today, a much longer period.
The authors state in their conclusion that they do not claim that the iPhone is the sole cause of the post-2007 decline, but they state that “the introduction of the modern smartphone played a sizeable role in the decline of US births.”
This is a strong claim, both the causal language and the implied magnitude of effects. For me, the strong conclusion doesn’t align with the strength of the evidence presented in the analysis.
Don’t let the facts get in the way of a good story
Of course, we all pump up the importance of our research findings to some extent. But I worry about how easily such plausible-sounding grand narratives, especially sold as a “natural experiment,” can become accepted by the media and public as established fact, precisely because they fit with a story we already believe. Policies aimed at restricting access to smartphones and social media among youth are also having a policy moment (which has its own challenges of causal inference), and I imagine this paper will be cited in support of specific policy agendas, for better or worse. It’s beyond my scope here to weigh in on the wisdom or likely effectiveness of certain policies, but my hope is that we can keep the standards of evidence for such policy decisions high (I know, what naïve, utopian world do I live in?!).
I am personally sympathetic to the idea that smartphones and social media have played a role in the social and demographic changes of the last twenty years. But I would be loathe to put any percentage on it, and I’m not sure we can ever credibly do that. My worry is that running with bold claims (based on shaky evidence) that the iPhone caused the baby bust risks oversimplifying the complex social dynamics surrounding fertility decisions, including the on-going relevance of how economic uncertainty affects family formation.
Bottom Line
Declining birth rates are real and genuinely poorly explained. Smartphones and accompanying social change likely played some role in the longer run, but this particular analysis doesn’t convincingly show that. The early iPhone roll-out coincided with the dramatic shock of the Great Recession. No econometric magic wand can cleanly separate the effects a new smartphone from the largest economic recession in eighty years.
Since this is a working paper, we’ll get a chance to see how the authors respond to the feedback they get in peer-review, and I’ll be interested to see the final version (though I doubt the media would revise their runaway headlines regardless). My genuine thanks to the authors for this thought-provoking work and for engaging with lots of the early feedback they are receiving on-line.
Regardless of the validity of causal estimates, on this Sunday afternoon, I encourage you to put your phone on Do-Not-Disturb, and go talk to some humans in real life!
Stay well,
Jenn
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Post-Script: A deeper dive for the methods-curious
The Identification Problem
As noted, AT&T coverage was not random, but highly correlated with income and population density, factors also correlated with fertility trends.
Empirical Approach #1: Entropy balanced Poisson event-study
The entropy balancing re-weights control counties to match treated counties on four observable county-level characteristics (within six urban/rural strata): the % of the Black population, % Hispanic population, % urban population, and the % 2008 Republican presidential vote share. What’s really telling is that the effective sample size of the new “balanced” control group is only 77 out of 1399 counties—highlighting the difficulty of finding valid comparison counties, even with this small list of demographic characteristics. The authors are transparent about this, but it’s a big red flag to me that it’s really hard to generate a good control group here.
Despite large median household income differences, economic variables were not included in balancing, but left for later as county-level fixed effects and time-varying regression controls. The justification seems to be that these time-varying economic controls account for the differential impact of the recession on counties. But it feels hard to simultaneously argue that the groups are so different as to require aggressive re-weighting on some covariates, but that standard regression controls will adequately absorb differential impacts of the same recession shock.
The county-level fixed effects used here will absorb stable differences between counties, like the fact that richer, more urban counties have lower baseline fertility. Time effects account for common shocks. Time-varying covariates can account for within-county changes over time, like how fertility changes when unemployment goes up.
But the approach doesn’t account for the key threat to causal inference here— that the trends in fertility between urban and rural counties may have been different in this period for many non-iPhone reasons. This could include an interaction between county characteristics and a common shock, like the recession. The housing crash was more heavily concentrated in metro areas. The model assumes there would be no differential fertility response to the recession, or no diverging trends for any other reason.
As mentioned above, the entropy balanced model ends up with an effective sample of 77 counties, meaning any county fixed effects are identified from within-county variation in those 77 effectively-weighted control counties plus the 914 treated counties. That’s a very narrow slice of data from which to use within-county variation to absorb both the treatment effect and confounding effects.
Empirical Approach #2: The Synthetic Diff-in-Diff (SDID)
The synthetic difference-in differences model also re-weights control counties, but this time to identify controls whose pre-treatment birth rate trajectory best matches the treated counties’ trajectories. This is the basic idea of the “parallel trends” assumption in diff-in-diff models: If treated and control counties tracked closely on fertility before the introduction of the iPhone, any differences afterwards are more credibly due to the iPhone (if nothing else changed in the meantime, of course).
The authors reveal very little about how treated and control counties look pre-trend or how the weighting changes this, so we have little to go on to assess what the weighting has done here. In addition, the pre-treatment window for matching trajectories was short (2003-2006) and covered a time when national fertility trends were quite flat. Abadie, et al caution that “when designing a synthetic control study, it is of crucial importance to collect information on the affected unit and the donor pool for a large pre-intervention window.” A short, flat pre-intervention window could make a lot of counties’ trajectories look like a reasonable match, simply because there isn’t enough variation in the pre-period to distinguish good vs bad synthetic controls in trajectories, and any good matches could be due to noise. This substantially weakens the credibility of the synthetic diff-in-diff model which relies on it’s ability to claim pre-2007 comparable trends and thus the causal impact of the iPhone thereafter, rather than other things that caused a national trends break in 2008.
Reconciling the two models
The entropy-balanced Poisson and the synthetic difference-in-differences estimators disagree by roughly a factor of two at the key ages: -4.5% vs -8.0% at ages 15–19; -3.2% vs -6.6% at ages 20–24. The authors attribute this difference to how the estimators handle pre-iPhone trends, but this highlights that different assumptions about pre-2007 trends are crucial to defining the appropriate counterfactual.
Placebo tests
I really like Placebo tests (aka negative controls), so I was prepared to be dazzled here. The general idea is that you re-run your analysis with a “pretend” treatment that shouldn’t have an effect (like a placebo). If the placebo does have an effect, you have good evidence that something else is going on and you are not picking up true causal effects. Conversely, if the placebo shows no effect, we have more confidence in the validity of the “experiment” our model is trying to mimic (though this is still not definitive evidence of that validity). For their placebo tests, the authors applied 1) placebo “timing”—what happened to fertility in high and low AT&T coverage counties before the iPhone came out? If the iPhones are the causal mechanism, the AT&T variable shouldn’t matter before 2008. 2) Carrier placebos. If the estimates are picking up something about counties that have high 3G coverage in general rather than the iPhone, this would may show up in counties with high coverage with Sprint or Verizon.
Despite my high hopes, these placebo tests did not bolster my confidence in the estimates.
Figure B.1. (SDID with placebo timing)
At ages 20–24, the placebo treatment years look like what you would hope for, with 2008 coefficients set apart from pre-treatment years. The visual is not quite as clean for ages 15-19, where the placebo years are trending in the same direction as the treatment year, albeit with smaller magnitudes. This gets a bit worse for 25-29 year olds, where the placebo coefficients are substantially negative — in some cases larger as than the 2008 estimate. The separation between placebo and treatment years above age 30 is not great.
Figure B.2: Entropy-Balanced Poisson Model
This is where things get more serious. The authors themselves report in the appendix: “at five of six age bands the largest placebo magnitude exceeds the true 2008 first-year coefficient.” So in five out of six age groups, the largest fake effect the entropy-balanced Poisson produces from pre-period data is bigger than the real iPhone effect the paper claims to have identified. It’s hard for me to interpret this as anything but a failure of the placebo tests, which implies the type of confounding by county-level variables that we are concerned about is important.
Figure B.4 (Verizon carrier placebo, SDID)
The Verizon 2008–2009 placebo at ages 15–19 and 20–24 is null, which is reassuring. But at ages 25–29, 30–34, and 35–39, the placebo is significantly negative, despite Verizon having neither the iPhone nor Android during that window. There is no smartphone-based explanation for these effects. The authors attribute them to “connectivity-tier differences among rural counties associated with diverging older-age fertility for reasons unrelated to the iPhone” ... but this is precisely the urban/rural fertility confound we are worried about.
Figure B.6 (Sprint carrier placebo, SDID)
The Sprint placebos at ages 20–24 are significant. Sprint had no iPhone and no Android during that window, so a significant negative effect at one of the two headline ages is not a good sign.
Taking all four placebo figures together: the SDID timing placebo works at ages 15–24 but generates large spurious pre-period effects at older ages; the Entropy-balanced Poisson timing placebo fails in five of six age bands; the Verizon carrier placebo generates significant spurious effects at 25–39; and the Sprint carrier placebo generates a significant spurious effect at the headline age of 20–24.
Overall, these are not confidence-inspiring placebo tests.
But there is also a more fundamental limitation of the “timing” placebo tests: they are estimated entirely on pre-2007 data, before the recession. A null pre-period placebo would be entirely consistent with a biased post-period estimate if the confound is a trend break in 2008 rather than a pre-existing divergence. Thus, these timing placebos can’t tell us whether the model correctly separates iPhone effects from recession effects in the post-period, because the recession isn’t in the placebo timing sample.
For the me, the most convincing placebo-like tests to address the threat of confounding by the Great Recession would be ones that use the same AT&T exposure but with different outcomes, such as other county-level measures that shouldn’t be causally impacted by the new iPhone (like unemployment, housing foreclosures, drug-overdose rates, etc). If the > AT&T variable also predicts lots of other county level outcomes over this period besides birth rates using the same exact models, that would be strong evidence for me that the iPhones themselves are not doing the work here. But—if you showed me that the AT&T coverage effect was very specific to fertility rates, I genuinely would be much persuaded by the plausibility of the causal claims here.
A few stray head scratching points for me....
A model restricted to just 2008-2009 (to avoid contamination by the Android smartphone roll-out) found similar iPhone effects, especially for 15-19 year olds. (Figure A8). Again, given the small number of iPhones with limited functionality in the first year of roll-out, this seems like a sure sign that something else is going on.
Figure A3 shows that the estimates don’t change that much using the fancy methods relative to a more basic population-weighted regression. Given the big differences in baseline characteristics between treatment and controls in Table 1, it feels less comforting to me that the fancier causal inference approaches look similar to a simple regression model. To me, this signals that they are all suffering from the same confounding problem.
Figure 5 shows that effects are similar for married and unmarried women, and for first vs. subsequent births. In such short time frame, it seems strange to me that that people already married or with kids would be as affected by new iPhones (but less surprising if a broader recession effect).
Looking more closely at the proposed mechanisms
Less socializing with peers
Intuitively, such displacement would require more than a small fraction of one’s peers to be opting out due to time with their iPhones.
Figure 9 in the working paper shows that national trends in time with friends were quite flat over the study period, while time alone actually decreases for the key 15-19 year old group.
The preferred SDID model estimates a sizeable drop in birth rates among 15-19-year-olds as early as 2008 (Figure 4). Since babies born in 2008 were largely conceived in 2007, that drop would require believing the iPhone had an almost immediate and big impact on 15-19 year fertility behavior, even with a very low % of iPhone ownership overall in those early months. Given the $499 plus $59.99/month two year contract, it’s unlikely 15-19 year-olds were a group most likely to have iPhones in these early months. Again, to me this implies something else is going on.
Lindberg, et al show that increases in contraception use rather than decreases in sex contributed the most to declining US teen fertility from 2007-2012, which doesn’t fit with the social displacement idea (thus putting all the eggs in the “information” channel below).
Pornography consumption substituting for partnered sex
This is another plausible argument for the longer-term societal impact of the internet and smartphones-- but not for the iPhone specifically from 2008-2011. As noted above, the iPhone was first on the “Edge” network, which was not much better than dial up. Reliable streaming speeds didn’t arrive until very late in the study window. Home-based pornography consumption was already available on home computers before the iPhone existed, and variation in AT&T cellular coverage wouldn’t be relevant to home use.
Access to information
Smartphones may make it easier to find out about and access birth control and abortion services. This is plausible in general, but again much less plausible in the study time frame specific to the roll-out of the iPhone. It’s true that a young woman in an AT&T covered county could have used the iPhone safari browser in 2007 to find information about emergency contraception or abortion. But as we’ve seen, a very low percentage of people had an iPhone in the early years (and likely lower in the 15-19 year old age group given the high price of iPhones). What’s more, it’s hard to see why this information channel would cause a sharp break from secular trends in contraceptive knowledge and access that were already underway and widely available on the internet before smartphones. A recent paper for example, examines the impact of widening internet access in the US on teen birth rates from 1999-2007, reflecting a much longer term process underlying this “information” channel. Figure 8 also shows that contraception at last sex was already rising nationally before 2007. The paper doesn’t show that this happened faster in AT&T served counties, so the “information channel” specific to the iPhone is only hypothetical, and it requires a lot for me believe such a mechanism could generate such large marginal effect so quickly.
That’s all for now, but if you had a different take on the results, I’d love to hear it!
This is an extraordinarily thoughtful dive into our paper---thank you! We're working on a revision that responds to your comments and criticisms in they detail they deserve, and I think it will be improved as a result. Long stories short, we agree with you that in an ideal world, we'd have random smartphone assignment. Since we don't live in that ideal world, we need to make the identifying assumptions using AT&T coverage as transparent as possible and to stress test the results every way we can. We're working on both, and the results of new robustness checks---including but not limited to adding population density-by-year fixed effects, extending the SDID pre-window, estimating by urban status, and placebo tests based on urban status within the control counties---are reassuring. While I think this holds up as solid evidence for an "it's (partly) the phones" story, I want to give you and others the evidence. So please stay tuned.
Your knowledge of statistical analysis is what prevails in so many of these situations where the standard science reporting in the popular media is willing to "jump" on nearly anything for a quick story. I would hope that your analysis becomes "breakout" reading beyond SubStack as its content often is critical. Kudos.