A study appearing in JAMA Pediatrics suggests that children born late-term have better cognitive outcomes than children born full-term. As if pregnant women didn’t have enough to worry about. For the video version of this post, click here.
Let’s dig into the data a bit, but first some terms (sorry for the pun). “Early term” means birth at 37 or 38 weeks gestation, “full term” 39 or 40 weeks, and “late term” 41 weeks. In other words, this study is not looking at pre-term or post-term babies, all of the children here were born in a normal range.
Ok, here’s how the study was done. Researchers used birth records from the state of Florida and linked them to standardized test performance in grades 3 through 10. Compared to children born at 39 or 40 weeks of gestation, those born at 41 weeks got test scores that were, on average, about 5% of a standard deviation higher. To get a sense of what the means, if these were IQ tests (they weren’t) that would translate to a little less than 1 IQ point difference. Not huge, but the sample size of over one million births makes it statistically significant.
10.3% of those born at 41 weeks were designated as “gifted” in school, compared to 10.0% of those born at full-term.
Before I look at what might go wrong in a study like this – is the effect plausible? To be honest, I sort of doubt it. One week extra development in utero certainly will lead to some differences at or near birth, but I find it hard to believe that any intelligence signal wouldn’t simply be washed away amid all the other factors that affect developing young minds prior to age 8.
Now, the authors did their best to adjust for some of these things – race, sex, socioeconomic status, birth order, but it seems likely that there are unmeasured factors here that might lead to longer gestation and better cognitive outcomes – maternal nutrition comes to mind, for example.
We also need to worry about systematic measurement error. These gestation times came from birth certificate data – in other words, many of these measurements may have been some doctors best guess. If the dates were determined by ultrasound, larger babies might be misclassified as later term. Also, I suspect that if conception dates weren’t well known, a lot of doctors filling out the birth certificate may have just written “40 weeks” to put something in that box.
The authors attempted to look just at women where the likelihood of prenatal care was high, finding similar results, but again, with the tiny effect size, any small systematic measurement error could lead to results like this.
The authors state that this information is relevant to women who are considering a planned cesarean or induction of labor. Currently, the American College of Obstetrics and Gynecology recommends “targeting” labor to 39-40 weeks to avoid some physical complications of late-term birth. In my opinion, having this study change that recommendation at all would be premature.
A study appearing in JAMA neurology links better Vitamin D level in pregnant women to a lower risk of multiple sclerosis in their offspring. There are some really impressive features of this study, but there are some equally impressive logical leaps that seem to defy the force of epidemiologic gravity. Let's give the study some sunlight.
For the video version of this post, click here.
The study was run out of Finland, which is a country that figured it might be a good idea to keep track of the health of its citizens. In fact, since 1983, nearly every pregnant woman in Finland has been registered, and a blood sample sent to a deep freezer in a national biobank. The researchers identified 193 individuals with MS, and went back into that biobank to measure their moms' vitamin D levels during pregnancy. They did the same thing with 326 controls who were matched on their date of birth, mother's age, and region of Finland.
This is from the first line of their discussion:
Wow. 90%. That sounds scary. And the news outlets seem to think it is scary too. But that impressive result hides a lot of statistical skullduggery.
Here's the thing, Vitamin D level is what we call a continuous variable. Your level can be 5, 10, 17, 42, whatever – any number within a typical range. When you study a continuous variable, you have to make some decisions. Should you chop up the variable into categories that others have defined (like deficient, insufficient, normal), or should you chop it up into even-sized groups? Or should you not chop it up at all?
As a general rule, you have the most power to see an effect when you don't chop at all. Breaking a continuous variable into groups loses information.
When the Vitamin D level was treated as the continuous variable it is, there was no significant relationship between Vitamin D level in mom and MS in the child. When the researchers chopped it into 5 groups, no group showed a significantly higher risk of MS compared to the group with the highest level. Only when they chopped the data into 3 groups did they find that mom's who were vitamin D deficient had 1.9 times the risk of those that were insufficient. That's the 90% figure, but the confidence interval ran from 20% to 300%.
And did I mention there was no accounting for mothers BMI, smoking, activity level, genetic factors, sun exposure or income in any of these models? Despite that, the paper's conclusion states :
That statement should go right on the jump to conclusions mat.
Look, I'm not hating on Vitamin D. I actually think it's good for you. But research that adds more to the hype and less to the knowledge is most definitely not.
Few aspects of modern medicine engender as much controversy as our labor and delivery practices. Rates of early induction of labor vary widely from country to country – even from hospital to hospital. And while some randomized trials have demonstrated that induction of labor prior to 40 weeks gestation might have favorable effects for infants with certain conditions like large-for-gestational age, we really don’t have much data on the effects of induction of labor during a normal pregnancy. But a study appearing in the New England Journal of Medicine attempts to shed light on that issue.
For the video version of this post, click here.
Run out of 39 hospitals in England, this study randomized 619 women, all age 35 or older on their first pregnancy, to labor induction at 39 weeks, or usual care.
Why do this? Well, for one thing, induction of labor prior to the official due date is pretty common. There is, perhaps, a quality-of-life argument to be made about having the ability to more or less choose when to deliver a baby. There is also some observational data that suggests that the sweet spot for delivery is around 38-39 weeks. Prior to that, complications associated with pre-term infants go up, and much beyond that and you start to see other birth complications.
Now, this study was clearly too small to detect differences in rare outcomes like neonatal or maternal mortality, but there has been some concern that induction of labor might increase the rate of c-section.
This study saw no such increase. The rate of c-section was 32% in the induction group and 33% in the usual care group – not statistically different. There were also no differences in rates of assisted vaginal delivery or NICU admissions, and every child in the study survived to hospital discharge. One fact caught my eye, though, and I think it gives us insight into the main limitation of this trial.
There was no significant difference in birth weight between the arms of the study. You’d think that the early induction arm would at least have slightly smaller babies. But in reality, the arms just weren’t that different in terms of any measured variables. Why? Well, there were women in the usual care arm who went into labor at 38 weeks. In fact, only 222 of the 305 women in the induction group got induction of labor prior to 40 weeks of gestation, as the protocol specified.
This bias, which the authors half-jokingly describe as “non-adherence”, is due to the fact that randomization into the study could occur at any time from 36-40 weeks. If you wanted to really answer the question that the authors pose, you’d randomize everyone at 39 weeks, and if they were put in the early induction arm, induce them at or near the time of randomization.
So we need to interpret this study not as saying that early induction is safe, but that a plan for early induction is safe. This is a subtle difference, for sure, but an important one if you are discussing inducing a woman who has already hit the 39 week mark. Still, in my book, a small victory for patient autonomy is a victory nonetheless.
Tuna, shark, king mackerel, tilefish, swordfish. If you’ve ever been pregnant, or known someone who has been pregnant, this list of seemingly random aquatic vertebrates is all too familiar to you. It’s the “avoid while pregnant” list of seafoods, and it’s just one of the confusing set of messages surrounding pregnancy and fish consumption.
(For the video version of this post, click here).
Because aren’t we supposed to be eating more fish? Fish are the main dietary source for omega-3 fatty acids, which can cross the placenta, and may promote healthy brain development. Of course, some of these fish contain mercury which, as Jeremy Piven taught us all, may be detrimental to cognitive development.
These contradictory facts led the US FDA, in 2014, to recommend that pregnant women consume more fish, but not more than 3 times a week. You have to love the government sometimes.
A study appearing in JAMA pediatrics is making some waves with its claim that high levels of fish consumption, more than 3 times per week during pregnancy, is associated with more rapid neonatal growth as well as higher BMIs throughout a child’s young life. Now, contrary to what your mother-in-law has been telling you, more rapid infant growth is not necessarily a good thing, as rapid infant growth is associated with overweight and obesity in childhood and adulthood.
But fish as the culprit here? That strikes me as a bit odd. Indeed, prior studies of antenatal fish consumption have shown beneficial or null effects on childhood weight gain. What is going on here?
The authors combined data from 15 pregnancy cohort studies across Europe and the US, leading to a final dataset including over 25,000 individuals. This is the studies greatest strength, but also its Achilles heel, as we’ll see in a moment.
But first the basic results. Fish consumption was based on a food frequency questionnaire, a survey instrument that I, and others, have a lot of concerns about. Women who reported eating less than or equal to 3 servings of fish a week had no increased risk of rapid infant growth or overweight kids. But among those eating more than 3 servings, there was around a 22% increased risk of rapid growth from birth to 2 and overweight at age 6.
These effects were pretty small, and, more importantly, ephemeral. The authors looked not only at the percentage of obese and overweight children, but the raw differences in weight. At 6 years, though the percent of overweight and obese kids was statistically higher, there was no significant weight difference between children of mothers who ate a lot of fish and those who didn’t. When statistics are weird like this, it usually suggests that the effect isn’t very robust.
In fact, this line from the stats section caught my eye, take a look:
That means the authors used numbers predicted by a statistical model to get the weight of the children rather than the actual weight of the children. I asked the study’s lead author, Dr. Leda Chatzi, about this unusual approach and she wrote “Not all cohorts had available data on child measurement at the specific time points of interest… in an effort to increase sample size and…power in our analyses, we…estimated predicted values of weight and height”.
So we have a statistical model that contains as a covariate, another statistical model. This compounds error into the final estimate, and in a study like this, where the effect size is razor thin, that can easily bias you into the realm of significance.
And, at this point it probably goes without saying, but studies looking at diet are always confounded. Always. While the authors adjusted for some things like maternal age, education, smoking, BMI and birth weight, there was no adjustment for things like socio-economic status, sunlight exposure, diabetes, race, or other dietary intake.
What have we learned? Certainly not, as the authors suggest, that
That they wrote this in a study with no measurement of said pollutants is what we call a reach.
Look, you probably don’t want to be eating fish with high levels of mercury when you are pregnant. But if my patients were choosing between a nice bit of salmon and a cheeseburger, well, this study doesn’t exactly tip the scales.
For the video version of this post, click here.
If you're a researcher trying to grab some headlines, pick any two of the following concepts and do a study that links them: depression, autism, pregnancy, Mediterranean diet, coffee-drinking, or vaccines. While I have yet to see a study tying all of the big 6 together, waves were made when a study appearing in JAMA pediatrics linked antidepressant use during pregnancy to autism in children.
To say the study, which trumpets an 87% increased risk of autism associated with antidepressant use, made a splash would be an understatement:
The Huffington post wrote:
The Daily telegraph, rounding up, said:
But if you're like me you want the details. And trust me, those details do not make a compelling case to go flushing all your fluoxetine if you catch my drift.
Researchers used administrative data from Quebec, Canada to identify around 145,000 Singleton births between 1998 and 2009. In around 3% of the births, the moms had been taking anti-depressants during at least a bit of the pregnancy. Of those kids, just over 1000 would be diagnosed with autism spectrum disorder in the first 6 years of life. But if you break it down by whether or not their mothers took antidepressants, you find that the rate of diagnosis was 1% in the antidepressant group compared to 0.7% in the non-antidepressant group. This unadjusted difference was just under the threshold of statistical significance by my calculation, at a p-value of 0.04.
These numbers aren't particularly overwhelming. How do the researchers get to that 87% increased risk? Well, they focus on those kids who were only exposed in the second and third trimester, where the rate of autism climbs up to 1.2%. It's not clear to me that this analysis was pre-specified. In fact, a prior study found that the risk of autism increases only when antidepressants are taken in the first trimester:
And I should point out that, again by my math, the 1.2% rate seen in those exposed during the 2nd and 3rd trimesters is not statistically different from the 1% rate seen in kids exposed in the first trimester. So focusing on the 2nd and 3rd trimester feels a bit like cherry picking.
And, as others have pointed out, that 87% is a relative increase in risk. The absolute change in risk remains quite small. If we believe the relationship as advertised, you'd need to treat about 200 women with antidepressants before you saw one extra case of autism.
But I'm not sure we should believe the relationship as advertised. Multiple factors may lead to antidepressant use and an increased risk of autism. Genetic factors, for example, were not controlled for, and some studies suggest that genes involved in depression may also be associated with autism. Other factors that weren't controlled for: smoking, BMI, paternal age, access to doctors. That last one is a biggie, in fact. Women who are taking any chronic medication likely have more interaction with the health care system. It seems fairly clear that your chances of getting an autism diagnosis increase with the more doctors you see. In fact, in a subanalysis which only looked at autism diagnoses that were confirmed by a neuropsychologist, the association with antidepressant use was no longer significant.
But there's a bigger issue, folks – when you take care of a pregnant woman, you have two patients. Trumpeting an 87% increased risk of autism based on un-compelling data will lead women to stop taking their antidepressants during pregnancy. And that may mean these women don't take as good care of themselves or their baby. In other words, more harm than good.
Could antidepressants increase the risk of autism? It's not impossible. But this study doesn't show us that. And because of the highly charged subject matter, responsible scientists, journalists, and physicians should be very clear. Women taking anti-depressants during pregnancy, do not stop until, at the very least, you have had a long discussion about the risks with your doctor.
For the video version of this post, click here.
Theres a reason why so few medications are recommended during pregnancy, and for the most part its not because we have evidence that they cause fetal harm. No, the reason so few drugs are recommended in pregnancy is because theyve never been tested in pregnant women. With the exception of a few medications explicitly designed for pregnancy, pregnant women are almost universally excluded from clinical trials.
So to determine if a drug may be harmful in pregnancy, we have to use observational data, and that means adjustment. This week, we can use a study appearing in the Journal of the American Medical Association as a perfect example.
Do anti-depressants, when used in pregnancy, increase the risk of persistent pulmonary hypertension of the newborn? PPHN is a very rare, but highly morbid condition whereby the fetal circulation persists after birth, leading to hypoxia, respiratory failure, and in about 10% of cases, death.
To determine if anti-depressants increase the risk of PPHN, a group of Harvard researchers used data from the Medicaid eXtract database, comprising almost 4 million pregnant women. Of those 4 million, about 130,000 had filled a prescription for an anti-depressant towards the end of pregnancy, mostly SSRIs. The rate of PPHN was 20 out of 10,000 births among those not taking anti-depressants, and 30 out of 10,000 births among those who did. Case closed?
Well, no. These women werent randomized to take anti-depressants, they took them for a reason, and lots of factors play into this: depression, obviously, but also personal beliefs, access to care, and any number of other confounders.
Enter adjustment. The authors worked very hard to identify a slew of confounders, and after accounting for them, the relationship between anti-depressants and PPHN went away. So it would seem that women who are more prone to take anti-depressants are more prone to have a child with PPHN, but the medications are not causal.
Unless...there was over-adjustment. Over-adjustment occurs when you statistically account for something that lies on the causal pathway between the exposure and outcome of interest. As an example, what if anti-depressants increase the risk of premature birth, which increases the risk of PPHN. Adjusting for prematurity would make it look like the medications were safe, when in fact they werent.
It can be hard to tease out. But theres a really important fact that we shouldnt forget here. All medications have risks, and all medications have benefits. Depression in a mother is a much, much greater risk to a newborn than PPHN.
Personally, I think the signal of harm is small enough to essentially be insignificant. For women with depression, these medications may, in fact, dramatically benefit both mother and baby.
Canadian researchers performed a large, cluster-randomized trial to try to reduce C-section rates in Quebec. The intervention was multi-faceted, ranging from education to auditing with physician feedback. A great example of a trial with a statistically significant, yet very discouraging results. The original article appears in the NEJM.
My take in 150 Seconds can be found here.