PNAS Just Published a Policy Brief. They're Calling It a Cohort Study.
Fatal flaws include... where do I start?
A paper dropped this morning in PNAS claiming that community water fluoridation has no effect on adolescent IQ or adult cognitive function. Within hours it was circulating as proof that the science is settled — that states like Utah and Florida made a mistake pulling fluoride from their water, and that critics of fluoridation are, once again, trafficking in discredited fear. The paper is authored by John Robert Warren and colleagues from the University of Minnesota and University of Wisconsin, using data from the Wisconsin Longitudinal Study. I’ve read it carefully. The conclusion is not supported by the methodology. Here are the reasons why, and here’s what the actual data show — including a number buried in the paper’s own table that the authors appear to hope you won’t look at too closely.
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Start with who is replicating whom. The paper describes itself as replicating and extending “Warren et al. (2025)” — a prior study in Science Advances that also found no fluoride-IQ association. The lead author of today’s PNAS paper is the same J.R. Warren. A scientist confirming his own prior finding, using the same dataset, at the same institution, is not replication. It is echo. Independent replication — the thing that actually moves scientific consensus — requires a different group, ideally with different data, in a different population. That has not happened here, regardless of how the paper is framed.
Now to the exposure variable, which is where everything falls apart.
Wrong Outcomes Measured
The fluoride exposure in this study is not measured in any child. There are no urinary fluoride levels. No serum fluoride concentrations. No dental fluorosis assessments. No water samples from the families’ actual taps. These are the measurements and outcomes used in studies to data. Instead, exposure is inferred from county-level historical records on when communities began water fluoridation programs — and, critically, from whether untreated wells in a county had naturally occurring fluoride levels deemed sufficient. Children whose counties had naturally sufficient well fluoride were classified as “exposed from birth.”
This matters enormously, and the paper treats it as a minor methodological footnote. Natural calcium fluoride (CaF₂) — what occurs in groundwater — and fluorosilicic acid (H₂SiF₆), the industrial byproduct of phosphate fertilizer manufacturing that is actually added to municipal water, are not the same compound. They differ in bioavailability, in the co-contaminants they carry, and in the chemical form that crosses biological membranes. The entire “exposed from birth” category in this study is largely populated by children who drank well water with natural calcium fluoride, not children who drank fluorosilicic acid from a treatment plant. Lumping these together as equivalent “fluoride exposure” is not a conservative methodological choice — it is a category error that makes the primary comparison scientifically incoherent.
Ecological Fallacy and SES Confounding
There is also the matter of what epidemiologists call the ecological fallacy. Assigning county-level exposure data to individuals and then analyzing it as if it were personal exposure history does not tell you about individuals — it tells you about counties. Every coefficient in the paper’s Figure 1 of this paper is built on county-level assignment, not individual measurement. When you run a regression on county-level proxies and find no association, you have learned something about county-level proxies. You have learned nothing definitive about what fluoride does in the developing brain. Studies of population averages tells us little to nothing about susceptibles.
Now look at their Table 1. The authors present their data honestly here, and it contains the answer to everything.
Model Under Specification
The “Exposed from Age 14” group — children whose communities began fluoridating when they were teenagers, after most of childhood brain development had already occurred — has the highest IQ scores in the entire sample. It also has the highest family income, the most educated fathers, the highest paternal occupational prestige, the fewest siblings, and the largest community size. Every single socioeconomic indicator moves in lockstep with the exposure gradient. Communities that fluoridated later were larger, wealthier, better-governed cities. Communities that never fluoridated were smaller, more rural, lower-income towns. After controlling for parental education, father’s occupation, family income, and community size — with data collected in 1957 — the authors find that CWF exposure is no longer associated with IQ. They present this as a finding. It is not a finding. It is the expected mathematical result when you apply an inadequate set of socioeconomic adjustments to a confound that runs deeper than those adjustments can reach.
Parental education and father’s occupation in 1957 do not capture school quality, nutritional access, healthcare utilization, environmental co-exposures, cognitive enrichment at home, or the hundred other ways that being raised in a mid-sized Wisconsin city differs from being raised on a Wisconsin farm. Residual confounding here is not a theoretical concern. It is visible in the raw numbers before any adjustment is applied. The study’s null result is explained by the study’s own table.
Covariate Relevance (Temporal Influence)
There is a further problem with those adjustments that the paper does not acknowledge. The control variables — family income, father's occupation, parental education, community size — were all collected in 1957, when participants were sixteen years old. But the exposure window the paper is testing begins at birth. That means the "confounders" were measured after years of alleged fluoride exposure had already elapsed. Family income and community size at age sixteen are not pre-exposure baseline measures. They are snapshots taken mid-exposure, downstream of the same social sorting that tracks with fluoridation status — larger, wealthier communities fluoridated earlier. When you adjust for a variable that may itself be a product of the exposure process, you are not controlling confounding. You are potentially blocking the causal path you are trying to test. A null result from that procedure is not reassuring. It is expected.
Selection Bias
There is also a population problem that compounds this called selection bias. The Wisconsin Longitudinal Study is a one-third random sample of Wisconsin high school graduates of 1957. Children who dropped out before graduation are not in this dataset. They never were. Children with lower cognitive function — who are precisely the population most likely to show neurotoxicant effects, as the international fluoride literature consistently finds — are systematically excluded. The study cannot detect harm in the most vulnerable children because it selected them out at the design stage.
Collider Bias
The survivor conditioning compounds further in the later-life analyses. Cognition at ages 53, 64, 72, and 80 is only observed in participants who survived to those ages and remained in the study. Survival itself is a common effect of early cognitive capacity and lifetime health trajectory — both of which are plausibly connected to early neurotoxicant exposure. When you condition on a variable influenced by both the exposure and the outcome, you open what epidemiologists call a collider path: a spurious statistical relationship that obscures the true one. Running cognitive analyses only in long-term survivors of a 1957 cohort is precisely this structure. The paper presents five cognitive outcomes across the life course as corroborating evidence. They are not independent. They are five measurements in an increasingly selected, survival-conditioned subsample, each one more filtered than the last.
Irrelevant Cohort
And the cohort is from 1957. These individuals were born around 1939 to 1943. Community water fluoridation was in its infancy during their childhoods; the modern standard of 0.7 mg/L wasn’t established until 2015. Fluoride toothpaste didn’t exist as a mass-market product. Formula reconstituted with fluoridated water — one of the highest infant fluoride exposures in modern pediatric life — was not part of the exposure picture. The policy question being debated right now concerns children in 2024, who receive fluoride from water, toothpaste, dental treatments, and processed food simultaneously. The total fluoride burden in the modern pediatric environment is categorically different from what Wisconsin children experienced in 1945. This cohort cannot answer the question it is being asked to answer.
People who’ve been following the fluoride literature here know that the NTP conducted a systematic review — published in 2024 — that concluded with moderate confidence that fluoride exposure is associated with lower IQ in children. The Taylor et al. meta-analysis in JAMA Pediatrics (2025), which this paper explicitly positions itself against, reached similar conclusions. Both of those analyses were designed to detect what this paper cannot: a signal in populations with individual-level exposure data, at doses relevant to current policy. Warren et al. dismisses those findings in a single paragraph, characterizing them as based on “extremely high dosages” that exceed CWF-relevant levels. That characterization is contestable. The Taylor meta-analysis examined studies across a range of exposures including those at CWF-relevant concentrations. This framing is rhetorical, not analytical.
Policy Advocacy Masquerading as Science
What is not contestable is what the paper’s own opening paragraph tells us about why it exists. The authors describe their study as a response to evidence “cited in recent decisions to end CWF in Utah, Florida, and elsewhere.” The paper was designed after those policy decisions were made, to counter them. It was received at the journal December 10, 2025, accepted March 5, 2026, and published April 13, 2026 — sixteen weeks from submission to publication in PNAS, for a paper whose stated purpose is to influence ongoing public health policy. That is a fast timeline. The conclusion — null effect, no harm from fluoridation — is the conclusion that protects an entrenched public health position. The study design is one that makes a null result nearly inevitable: ecological exposure proxy, confounded comparison groups, selection-biased sample, inadequate SES adjustment, and the conflation of natural and added fluoride as equivalent exposures.
A properly designed study that wanted to answer this question would enroll children prospectively, collect urinary fluoride biomarkers at multiple developmental timepoints, separately analyze children who receive fluorosilicic acid from children who receive naturally occurring fluoride, include children across the full cognitive distribution including those who do not complete secondary school, and control for total fluoride burden rather than water source alone. No such study has been done in the United States at population scale. That is not an accident. It is the gap that this literature keeps successfully avoiding.
The question the field refuses to ask directly is this: if community water fluoridation is as safe as its defenders claim, why does the highest-quality prospective evidence consistently use ecological proxies rather than biomarkers? Why does the strongest null-result evidence keep coming from the same research group reconfirming its own prior work? Why does the NTP review — a review commissioned by the federal government, conducted by scientists with no financial interest in ending fluoridation — find moderate-confidence evidence of harm, while the studies deployed to dismiss it rely on 1957 cohorts and county-level exposure assignments?
The answer to that question is one this paper cannot provide. But the pattern itself is now strong enough to observe. I’ve been tracking it across the “public health” literature for years. It has a consistent shape: methodological choices that make null results structurally likely, paired with advocacy framing that presents those null results as definitive safety evidence. That pattern is what got fluoride into the American water supply without a prospective safety trial in the first place. It is the same pattern being deployed today to keep it there.
The next piece in this sequence will look at what the dose-response literature actually shows at concentrations between 0.5 and 1.5 mg/L — the range that includes current CWF levels — and why the threshold debate is far less settled than today’s PNAS paper implies.
Of course, NBC News and other outlets gleefully reported this non-study as the “longest”, not the “most irrelevant and warped piece of fish ever wrapped in the newspaper”, as it should have been reported.
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A lot.
Thanks yet again for exposing how (some - much - most?) of "modern science" works!
Great analysis. As the Research Director for the Fluoride Action Network I had been working on my own analysis of this paper before seeing yours, but my conclusion is the same: this study was incapable of detecting neurotoxicity from prenatal and early childhood fluoride exposure, which is exactly the life stage that almost all the 70+ studies of fluoride (F) and IQ have consistently found associated with reduced IQ.
Here are the problems I identified with the study, some of which are identical to what you identify:
There are three main reasons why this study likely could not have been able to detect an effect of F on IQ:
1.) The IQ tests were given to high school students in 1956 when they were 16 years old, so they would have been born in 1940. That is 5 years before the first artificial fluoridation trial in the US had even begun, so not a single person in this dataset had prenatal exposure from fluoridated water, or childhood exposure to fluoridated water from birth to past age 5 years. Almost all prior studies finding neurotoxicity found it from prenatal or early childhood F exposure. By age 5+ fluoride may have little effect on IQ. This study is incapable of assessing whether F is a developmental neurotoxicant.
2.) It measured IQ at an older age (16 y or even older) when it becomes difficult to detect a neurotoxic effect that occurred in utero or early infancy for several reasons even if there had been early life F exposure.
3.) It had only group-level fluoridation exposure information, and not even at a small local level but only at the level of a county in some cases and a school district in other cases. A 1969 US Public Health Service report shows that only about 3% of the population of Wisconsin had drinking water with naturally elevated water F above 0.7 mg/L. Combine that with the fact that there was no artificial fluoridation anywhere in the US for the first 5 years of life for this cohort and we can say that this study is incapable of detecting developmental neurotoxicity from either artificial or naturally occurring F in drinking water.
Limitations 2) and 3) produce greater random measurement error, with the age 16y IQ tests producing greater random (non-differential) error in the IQ score outcome measure and the group-level F exposure producing random error in the F status exposure measure. Combine both of these random errors and there is likely too much "noise" to detect a "signal" from an effect of F on IQ.