An odds ratio of 0.40 for placental abruption, confidence interval 0.29 to 0.57, drawn from 894,986 pregnancies. Stimulants, this says, cut the risk of placental abruption by 60 percent compared to nonstimulants.
That is the kind of number that reads like an answer. Tight interval. Enormous sample. A clean direction of effect.
Now read the commentary published alongside it, in the same journal, by an epidemiologist at the Norwegian Institute of Public Health. It spends most of its space explaining why you should not believe that number.
That gap—between a crisp finding and its own accompanying author's caution—is the whole problem in miniature.
Last week this column covered the widening gap between surging maternal ADHD treatment and the safety data meant to guide it. This week the data arrived, in the form of two specific obstetric-risk papers and a critique of causal inference itself. The trouble is that the biggest of those papers looks far more decisive than it is.
Start with what the Babinski and Tuan study actually did. Using TriNetX electronic health records, it compared stimulant and nonstimulant treatment during pregnancy across obstetric outcomes, adjusting for measured confounders with inverse probability of treatment weighting.
The head-to-head results are specific and confident. Stimulants versus nonstimulants: placental abruption 0.40, IUGR 0.66, preterm delivery 0.47, and placenta previa going the other way at 2.30, interval 1.82 to 2.91.
Precise, confident, and possibly meaningless. Here is why.
The comparison assumes the two groups differ mainly in which drug they took. But to isolate a drug effect, you need the groups to be otherwise alike—especially alike in the thing being treated.
They were not. ADHD was recorded in the records of only 47 percent of stimulant users and 15 percent of nonstimulant users.
Sit with that second figure. In the group defined by taking a nonstimulant ADHD medication, five out of six patients had no ADHD diagnosis in the record at all.
That is not a rounding problem. It means the propensity model was adjusting for an "ADHD" variable that was absent for most of the people it was supposed to describe.
And it means the two arms are not "same patient, different drug." They differ systematically in ways the model cannot see.
Consider how nonstimulants get prescribed. Per the Norwegian-Swedish commentary in this same literature, atomoxetine is typically neither first- nor second-line—it is what you reach for when methylphenidate or amphetamines fail, are poorly tolerated, or raise misuse concerns.
So "stimulant versus nonstimulant" partly encodes "first-line patient versus treatment-refractory patient." Different severity, different comorbidity, different everything. The odds ratio measures who gets which drug at least as much as what the drug does.
This is confounding by indication, and its nastier cousin, confounding by severity—where not just the disease but its intensity drives both the treatment choice and the outcome.
Now the crucial move: this is not a problem you fix with more data.
TriNetX's scale—nearly 900,000 pregnancies—buys precision. It does not buy validity. Those are different currencies, and the study spends the first as if it were the second.
A larger sample shrinks the confidence interval around an estimate. It does nothing to the bias baked into that estimate. If the comparison groups differ in unmeasured ways, the true target of your estimate is wrong, and collecting a million more records only pins you more tightly to the wrong number.
A larger sample shrinks the confidence interval around an estimate. It does nothing to the bias baked into that estimate.
That is why precision on a biased estimate is worse than useless. It launders uncertainty into false confidence. A wide interval at least announces its own doubt; a tight one around a contaminated comparison hands the clinician a decimal point that was never earned.
The commentary makes the same point in methodological language: p-values should not guide interpretation of importance. What matters is how well the study handled confounding, the strength of the estimate, and consistency with existing literature. On the first count, the head-to-head comparison fails.
We are not guessing about what adjustment does to these associations. We have watched it happen.
Camacho and colleagues ran the experiment across two jurisdictions—Ontario and New South Wales, nearly 700,000 pregnancies combined. Crude analyses showed elevated risk for nearly every outcome, odds ratios running 1.15 to 2.16.
Then they applied inverse probability weighting. Nearly all of those associations collapsed toward null.
One survived: pre-eclampsia, reportedly weighted OR 2.02, interval 1.42 to 2.88 in Ontario—though even that attenuated in New South Wales and further still when restricted to a subgroup with richer confounder data. Their conclusion was that psychostimulant exposure is "not a major causal factor for most measured outcomes."
That is the canonical demonstration. Adjustment eats the association. The crude signal was mostly confounding, and only the pre-eclampsia finding was stubborn enough to look like it might be real.
So when a study reports a battery of confident head-to-head odds ratios after adjustment, the prior should be skepticism, not the reverse. We have already seen these numbers dissolve under scrutiny.
Which raises the obvious question: is there any design that survives?
Yes—one. Stop comparing treated to untreated. Compare women who continued ADHD medication into pregnancy against women who discontinued just before it.
Per the Norwegian-Swedish commentary, Srinivas and colleagues did exactly this, using Norwegian and Swedish registries and more than 11,000 pregnant women with ADHD. Persistent users—at least two prescription fills in the first half of pregnancy—had a 9.8 percent rate of preterm birth. Discontinuers reportedly had 6.1 percent.
The elegance is in the denominator. Both groups have ADHD. The indication is present on both sides, so it cancels out—the diagnosis can no longer masquerade as a drug effect, because everyone in the comparison shares it.
That is precisely the confounding that sank the head-to-head comparison, engineered away by design rather than begged away by adjustment.
Note this design is not perfect. Confounding by severity can persist: the woman who continues may differ from the woman who stops in how badly she needs the drug. But it removes the crude contamination—having ADHD versus not—that the 47/15 split leaves wide open.
So what is the honest set of inputs a clinician can bring to a decision?
First, a robust and repeated signal: ADHD itself predicts adverse pregnancy outcomes, and preterm birth in particular shows up across settings, in the continue-versus-discontinue design where the diagnosis cannot be the confounder. That signal deserves weight.
Second, a shaky drug-specific signal: the confident head-to-head odds ratios, which mostly measure who gets which drug, and which the Camacho pattern suggests will not survive honest adjustment. That signal deserves suspicion.
Third, the absence that governs everything: no randomized data, and none coming. There is no FDA-approved ADHD medication for pregnancy, and there will be no trial to settle this.
Shared decision-making with those three inputs looks concrete. It starts before conception where possible. It treats untreated ADHD as a genuine risk, not a safe default. And it frames the choice as continue-versus-cease—the question the surviving design actually answers—rather than treated-versus-untreated, the question the seductive number only pretends to.
Last issue left open whether this continue-versus-cease logic would enter formal perinatal guidelines; the field is now openly asking whether it is time, and the honest answer is that the one defensible design should anchor those guidelines before the precise-looking one gets there first.
The 0.40 will keep circulating, because a tight interval on a huge sample is hard to argue with in a hallway. The discipline is remembering that it answers a question no patient is actually asking.