Audience: Parents, caregivers, clinicians, and readers assessing vaccine claims
Primary topic: MMR vaccination and autism diagnoses in early childhood
Source: Burstain and colleagues, The Pediatric Infectious Disease Journal, 2026. Read the source PDF | Journal article via DOI
Review boundary: Level A access to the full nine-page main paper, including its figures and tables. The linked supplementary appendix was inaccessible and has not been reviewed.
MMR vaccination and autism: What a study of 2.5 million children actually found
A large US study found no increased rate of recorded childhood autism diagnoses after first MMR vaccination before age 2. Understanding that reassuring result requires separating the size of the database from the quality of the comparisons made within it.
What This Study Teaches Us
This retrospective cohort study examined vaccination and diagnosis records for 2,560,035 children, finding a primary adjusted hazard ratio of 0.97 for childhood autism after first MMR vaccination between 11.5 and 24 months, with a 99% confidence interval of 0.91 to 1.03. In everyday language, its main analysis did not find a higher rate of recorded autism diagnoses among vaccinated children. The finding agrees with previous large studies, but unequal follow-up, incomplete records, missing family history, and unclear details of the timing analysis limit how much this paper can establish by itself. Its contribution is additional evidence against an increased association in the studied population, rather than a guarantee covering every vaccine outcome or every individual child.
Why This Matters
For patients and families: A parent can accurately remember noticing a developmental change after a vaccination without that sequence establishing what caused the change. This paper asks whether vaccination was followed by more recorded autism diagnoses across a large comparison population. It found no increased rate in its primary adjusted analysis. That finding deserves a clear explanation, while concerns about an individual child still deserve careful listening and appropriate developmental assessment.
For clinicians: The useful conversation starts with what was actually measured: the first MMR or MMR-varicella dose, a specific childhood autism diagnosis code, and the clinical records available afterward. It also distinguishes the main null result from lower estimates in two later vaccination windows. Those lower estimates do not establish that MMR prevents autism or that delaying vaccination offers a developmental advantage.
For policy and research readers: A study containing millions of records can estimate some associations precisely while retaining systematic errors. This paper illustrates why follow-up, data completeness, exposure timing, and the definition of the comparison group matter as much as the headline sample size. Its findings strengthen an existing evidence base; its reporting gaps are reasons to improve the analysis and documentation, not evidence that the opposite result occurred.
Study Snapshot
| Study type | Retrospective, observational cohort study with age-based landmark analyses and Cox regression. |
|---|---|
| Population | US children in the Epic Cosmos EHR database with linked birth-parent records, qualifying pediatric or family medicine visits between 12 and 24 months, and an active-patient designation. |
| Sample size | 2,560,035 children in the overall selected cohort; the main paper does not clearly provide each fitted model’s analytic denominator. |
| Study period | Clinical records from January 1, 2015, through December 31, 2024. |
| Exposure | First documented MMR or MMR-varicella vaccination between 11.5 and 24 months, also examined in five narrower age windows; administered and historically documented doses were included. |
| Comparator | Children described in the landmark methods as remaining unvaccinated during follow-up. The handling of later vaccination and the precise comparator denominator require clarification. |
| Primary outcome | First recorded encounter diagnosis of childhood autism, ICD-10-CM F84.0, after the relevant landmark. This is narrower than all autism spectrum diagnoses. |
| Follow-up | Follow-up could extend to age 8 but ended earlier at diagnosis, the last recorded encounter, or the study cutoff. Median reported follow-up was 853 days for children vaccinated at any age and 366 days for unvaccinated children. |
| Primary result | Adjusted hazard ratio 0.97; 99% confidence interval 0.91 to 1.03; reported P value 0.16. |
| Bias check | Pneumococcal conjugate vaccine booster at 12 to 15 months: adjusted hazard ratio 1.01; 99% confidence interval 0.99 to 1.04. |
| Journal and year | The Pediatric Infectious Disease Journal, 2026; published online July 28, 2026, ahead of print. |
| DOI and PMID | DOI: 10.1097/INF.0000000000005349. PMID: 42520244. |
| Funding and conflicts | The authors state that they have no funding or conflicts of interest to disclose. |
| Code and AI disclosure | The authors disclose ChatGPT assistance with code and manuscript drafting, with author review. Data and code are available on request to eligible Cosmos users, subject to platform restrictions. |
Clinical Bottom Line
The primary analysis found no increased rate of coded childhood autism after first MMR vaccination before age 2, consistent with previous research. This study does not provide evidence that delaying MMR reduces autism risk. Its observational design and reporting uncertainties also mean it should not be used to claim that MMR prevents autism or that this one analysis establishes complete vaccine safety.
What This Paper Looked At: MMR vaccination and autism
The researchers looked backward through existing medical records. They did not assign children to vaccination or withhold vaccination, and they did not examine every child personally. They assembled a group of children whose records could connect early vaccination history, subsequent encounter diagnoses, and information about the pregnancy and birth.
Eligibility required a primary care office visit between 12 and 24 months, an active-patient designation based on face-to-face encounters, and a linked record for the parent who carried the pregnancy. Children with a recorded autism diagnosis at or before 11 months were excluded. Figure 3 also shows that the final sample was restricted to children alive at the end of the study and recorded as male or female.
The authors used six age-window comparisons. Their stated goal was to compare children at similar developmental ages, because the timing of vaccination and the timing of autism diagnosis both matter. Each window represented a separate analytic cohort, rather than a simple subdivision of one identical comparison.
Three methods, translated into ordinary language
Landmark analysis: Choose a particular age as a starting point, establish which children meet the comparison criteria, and then examine later diagnoses. For this to work as intended, the rules determining vaccine status and the beginning of outcome follow-up must line up. The paper describes this intention, but its main text leaves important implementation details unresolved.
A causal diagram, or DAG: Draw a map of factors that might influence both vaccination and autism diagnosis, then use that map to choose adjustment variables. The main methods list neighborhood deprivation, race, ethnicity, geography, maternal age, gestational age, birth count, size at birth, and diabetes or genitourinary infection during pregnancy. Such a diagram makes assumptions visible; it cannot measure information absent from the records.
A negative control: Repeat the comparison using another exposure that is not expected to cause the outcome, but shares some healthcare patterns. Here, that exposure was a pneumococcal vaccine booster at 12 to 15 months. A similar near-null result is a useful check for certain biases, although it cannot certify that every source of bias has been eliminated.
What the Paper Found
There were 65,219 recorded childhood autism diagnoses in the overall selected cohort, representing 2.55% of that cohort. The median age at recorded diagnosis was 3.13 years. These are descriptive figures for the selected records, not a national prevalence estimate or a vaccinated-versus-unvaccinated absolute risk comparison.
Table 1 reports that 2,340,606 children received their first MMR dose between 11.5 and 24 months. The main adjusted comparison for that window produced a hazard ratio of 0.97, with a 99% confidence interval of 0.91 to 1.03. The unadjusted estimate was 0.92, moving closer to 1 after adjustment, a useful reminder that differences between the groups influenced the initial comparison.
The age-window results
| First-dose age window | Adjusted hazard ratio | 99% confidence interval |
|---|---|---|
| 11.5 to 24 months, primary analysis | 0.97 | 0.91 to 1.03 |
| 11.5 to 12.5 months | 0.98 | 0.93 to 1.04 |
| 12.5 to 13.5 months | 0.98 | 0.93 to 1.05 |
| 13.5 to 14.5 months | 0.98 | 0.91 to 1.05 |
| 14.5 to 17.5 months | 0.90 | 0.84 to 0.97 |
| 17.5 to 24 months | 0.92 | 0.85 to 0.99 |
None of these comparisons reported a statistically significant increase. The two later vaccination windows had estimates below 1 with intervals also below 1. Those are lower observed diagnosis hazards in those comparisons, not proof of protection or evidence for an optimal vaccination age. The separate windows used different analytic populations and should not be treated as a randomized contest between vaccination schedules.
How to read 0.97 without turning it into a misleading claim
A hazard ratio compares the rate of a first recorded diagnosis among children still under observation and not yet diagnosed. A value of 1 represents equal estimated hazards. The primary value of 0.97 corresponds to a 3% lower estimated hazard, but its uncertainty interval includes 1, so the study does not establish a lower hazard in the primary comparison.
The 99% confidence interval runs from 0.91 to 1.03. Under the fitted model and its assumptions, that interval spans approximately a 9% lower to a 3% higher relative diagnosis hazard. It is not a range of percentage-point changes in a child’s absolute autism risk, and it does not mean there is a 99% probability that the true effect lies inside this particular interval. Confidence intervals describe statistical uncertainty under assumptions; they do not include every possible error caused by incomplete records or biased comparisons.
The primary P value of 0.16 is also not the probability that MMR causes autism, nor the probability that the authors’ conclusion is correct. It indicates that the primary comparison did not cross the authors’ chosen statistical threshold. The estimate, its interval, and the study design are more informative than that single number.
What happened when the analysis was changed?
Adding further birth-related and congenital variables produced an adjusted hazard ratio of 0.97, with a 99% confidence interval of 0.92 to 1.03. Removing the neighborhood deprivation variable produced 0.96, with a 99% interval of 0.91 to 1.02. The pneumococcal booster comparison yielded 1.01, with a 99% interval of 0.99 to 1.04. These checks did not produce an increased MMR association.
Excluding 5,738 children with only one autism-coded encounter also yielded a similar adjusted estimate. However, that section reports an adjusted odds ratio of 0.97 with a 95% confidence interval of 0.91 to 1.03, rather than the primary hazard ratio with a 99% interval. Those are different statistical measures and should not be described as an identical repeat of the main model.
How Strong Is This Evidence
This is a substantial observational contribution to a question already investigated in other large populations. Its strengths include a large selected cohort, actual clinical vaccination documentation, age-specific comparisons, birth-parent information, sensitivity analyses, and a negative-control comparison. Together, those features make the reported primary null result worth taking seriously.
Its numerical precision is greater than its ability to establish causality. A large sample reduces some random uncertainty; it does not repair a missing diagnosis, an incompletely measured confounder, or a misaligned follow-up clock. Because the supplementary appendix and analytic code were not reviewed, the claim that landmark methods successfully removed time-related bias cannot be independently verified here.
The evidentiary weight is therefore best stated in two layers: this paper reports another large population-level comparison without an increased MMR association, while the broader peer-reviewed literature supplies the more durable context. Some uncertainties concern this paper’s reporting and implementation. They do not erase findings obtained independently in other cohorts.
Where This Paper Deserves Skepticism
The concerns below come from the paper’s stated limitations, its tables and figures, and a methods review of the supplied main text. Where implementation is unclear, that uncertainty is identified rather than treated as a demonstrated error.
1. Follow-up was substantially unequal
The paper reports median follow-up of 853 days among children vaccinated at any age, compared with 366 days among unvaccinated children. An unvaccinated child whose record ends before a later diagnosis cannot contribute that diagnosis to the database. Cox regression can accommodate different observed follow-up lengths, but it relies on assumptions about why observation ends. The authors assume censoring is noninformative after accounting for measured variables; that assumption is not guaranteed by the model itself. The authors suggest shorter unvaccinated follow-up could inflate apparent diagnosis rates in vaccinated children, but the combined direction of all biases cannot be established from this comparison alone.
2. The starting clock and exposure rules need clarification
The population methods begin follow-up at the first qualifying visit after 12 months; the landmark section begins it at the landmark age; Table 4 describes follow-up from vaccination for vaccinated children and from the first post-12-month office visit for unvaccinated children. The discussion also describes controls as unvaccinated at the same age, whereas the landmark methods describe controls as remaining unvaccinated during follow-up. These descriptions may refer to different summaries or implementation steps, but the main paper does not reconcile them.
3. A landmark label does not establish that timing bias disappeared
The main text describes classifying exposure by receipt of vaccination within an age window while beginning follow-up at the landmark age. If future vaccination information is used to label earlier observation time, the handling of diagnoses before vaccination becomes crucial. Likewise, requiring a control to remain unvaccinated throughout follow-up can select that group using later information. Clear risk-set definitions, handling of later doses, and the analytic code are needed to assess these possibilities. This is an unresolved methods concern, not a finding that a particular bias definitely occurred. The general importance of aligning exposure and follow-up is described by Suissa’s peer-reviewed methods analysis.
4. The missing-data description is internally inconsistent
The methods say neighborhood deprivation data were missing in 53% of the cohort. Table 1 instead lists 1,403,538 children with that measure recorded, or 54.82% of the total, implying approximately 45.18% missing by that denominator. The main text does not clearly explain whether the model used complete cases, imputation, or another approach. It also does not provide a clear fitted-model denominator for each comparison. The similar result after dropping the variable is reassuring, but it does not reconcile the discrepancy or show that excluded or incompletely measured children were interchangeable with the rest.
5. The diagram and adjustment list do not fully match
Figure 1 depicts sex among the proposed confounders. The primary adjustment set listed in the methods and Table 2 does not include sex. It is unclear whether sex was included in code and omitted from the written list, handled elsewhere, or left out of the fitted model. This discrepancy warrants clarification; it does not show how much the result would change. A causal diagram is useful only when readers can connect its assumptions to the actual analysis.
6. Family history and early developmental concerns were not fully captured
The authors acknowledge that family history of autism was unavailable. If families with greater underlying autism risk are less likely to vaccinate, that could concentrate higher-risk children in the unvaccinated comparison group and pull the vaccine estimate downward. Early concerns could also influence vaccination decisions before a formal diagnosis appears. The authors’ assertion that missing family history is unlikely to explain the near-null result is stronger than can be established without measuring those factors. The actual direction and magnitude depend on the relationships in this dataset.
7. A recorded diagnosis is not the date autism began
The outcome was an encounter code, F84.0. A child’s first coded encounter can occur after earlier developmental differences, evaluations, or diagnoses outside participating systems. The study did not provide a fresh specialist assessment of every child. Restricting to this code also means the analysis does not cover every autism spectrum diagnosis. Removing single-code cases helps address one aspect of misclassification, while leaving delayed recognition and uncaptured care unresolved.
8. The sample was selected, rather than a census of US children
Figure 3 shows that linked birth-parent records were available for roughly half of children reaching that eligibility step. Requiring visits, active status, linkage, and survival to the study’s end selects a particular population. Geographic representation was also uneven: Table 1 shows substantially different regional proportions from its benchmarks. The cohort is large and multisite, but the paper’s statement that it is broadly representative should not be equated with random national sampling.
9. The negative control cannot measure every remaining bias
The near-null pneumococcal estimate is helpful because it checks whether the framework produces an obvious association for another vaccine given at a similar age. Its value depends on assumptions about shared confounding and outcome ascertainment. MMR-specific decisions could differ from pneumococcal decisions, and different biases can offset one another. A negative-control result near 1 therefore does not establish that residual confounding is minimal or that the primary estimate is unbiased.
The main paper does not give a straightforward comparison of absolute diagnosis risk at a common follow-up age, with vaccinated and unvaccinated event counts and denominators for each fitted landmark model. Children could be followed up to age 8, but many were observed for much less time. The supplemental appendix was inaccessible, and the underlying data and code are restricted to eligible Cosmos users. These limits prevent independent confirmation of several details, although they do not negate the findings reported in the main tables.
What This Paper Does Not Show
It does not show that MMR causes autism. No age-window comparison reported a statistically significant increased diagnosis hazard, and the primary adjusted comparison was close to 1.
It does not show that MMR prevents autism. The lower estimates in later windows are observational associations within separate selected populations. They cannot justify a claim of prevention or a recommendation to delay vaccination.
It does not establish an individual child’s developmental history. A record-based population comparison cannot determine why a particular child experienced regression, when that child’s developmental differences began, or whether another diagnosis needs investigation.
It does not answer every vaccine safety question. The study examined a specific autism diagnosis code after a first MMR-containing dose. It did not test all vaccines, every formulation or schedule, every adverse event, or every subgroup. It also did not establish that every child had complete follow-up to age 8.
It does not make autism treatment claims. No cannabis, CBD, or other autism treatment was evaluated. Findings about vaccination cannot be used to infer treatment benefits. Questions about clinical care require their own evidence.
How This Fits With the Broader Clinical Conversation
The main result aligns with earlier research conducted in different settings. That agreement matters because independently assembled datasets can have different strengths and limitations. Confidence should come from the pattern across studies, with attention to study quality, rather than from a single large headline.
Denmark, 2019: Hviid and colleagues studied 657,461 children using national registries. The adjusted hazard ratio was 0.93, with a 95% confidence interval of 0.85 to 1.02. They did not find an increased MMR association overall, in analyses involving sibling history and other risk factors, or during specified post-vaccination periods. This comparison addresses some questions the new EHR dataset could not measure. Read the peer-reviewed cohort study.
United States, 2015: Jain and colleagues examined privately insured children with older siblings, including families in which the older sibling had autism. They found no increased association with MMR receipt regardless of the older sibling’s autism status. Family-history questions should therefore be discussed using studies that actually measured family history, rather than claiming that the new cohort answered them. Read the original investigation, including its published correction.
Systematic review, 2021: Di Pietrantonj and colleagues’ Cochrane review reported no evidence of an association between MMR immunization and autism. Its broader safety assessment also considered outcomes other than autism, illustrating why an autism result should not be expanded into a claim that vaccines have no adverse effects. Read the systematic review.
For further discussion on this site, see the autism and vaccination explainer. It is a companion educational page; the scientific basis for the comparisons above is the peer-reviewed literature cited here.
Dr. Caplan’s Take
When a parent describes a change in their child, I want to understand exactly what they noticed and when. The sequence matters for the child’s evaluation, even when it does not establish a cause. This paper adds a large comparison in which first MMR vaccination before age 2 was not followed by an increased rate of recorded childhood autism. That is useful information to bring into a conversation that can otherwise become dominated by fear.
I also want the methods to receive the same attention as the conclusion. The unequal follow-up is substantial. Some of the descriptions of timing and adjustment do not fully agree, and the missing-data figures need clarification. These are appropriate questions to ask of a reassuring study. Applying careful standards consistently makes the reassurance more credible, especially when the main finding agrees with independent research.
I would explain to families that this paper provides no evidence that delaying MMR lowers autism risk. At the same time, it should never be used to dismiss a developmental concern, postpone an evaluation, or suggest that a population statistic explains a particular child. The clinical task remains to understand the child in front of us, use the broader evidence when discussing vaccination, and be honest about what any individual study can establish.
What a Careful Reader Should Take Away
The main result is reassuring: this large retrospective study found no increased rate of recorded childhood autism after first MMR vaccination before age 2. Its findings fit the direction of previous large cohorts and systematic review evidence. The paper also contains enough uncertainty about follow-up, missing data, and analytic implementation to warrant a measured assessment rather than a claim of perfect methods.
The most defensible interpretation preserves both points. There is additional evidence against an increased MMR-autism association in the studied population, and there are specific questions the authors should clarify. Those questions do not establish vaccine harm, vaccine protection against autism, or a reason to delay vaccination.
Read This Paper Through Eight Different Lenses
Explore the perspectives below. Each interpretation keeps this MMR study’s finding tied to its evidence and limitations.
Patient Takeaway
Patient Takeaway
If your concern is whether an MMR vaccination could explain a change you noticed in your child, this study offers a population comparison. Among the children included in its records, first vaccination before age 2 was not associated with an increased rate of recorded childhood autism in the primary adjusted analysis. That finding agrees with the earlier studies discussed in this review.
The study did not examine every child personally, and a diagnosis entered in a chart is not the same event as the first developmental difference a family notices. A large database therefore cannot reconstruct one child’s story. It can help assess whether the proposed association appears across many children.
The useful takeaway is reassurance about the association studied, alongside continued attention to individual developmental concerns. The paper offers no evidence that delaying MMR reduces autism risk, and it does not evaluate every possible vaccine reaction.
Clinician’s POV
Clinician’s POV
A useful exam-room explanation starts with the question the study actually answered: did children with a first documented MMR or MMR-varicella dose between 11.5 and 24 months have a higher subsequent hazard of an F84.0 encounter diagnosis? The primary adjusted estimate was close to 1 and did not show an increase.
That language keeps the outcome, timing, and observational design visible. It also prevents two common counseling errors: treating the smaller estimates in later vaccination windows as evidence of prevention, and treating the paper as a guarantee about every vaccine outcome.
A family’s concern can be discussed alongside this result without implying that the result explains their child. The independent cohort and review evidence provide context, while the paper’s unequal follow-up and reporting questions deserve acknowledgment. Its practical clinical contribution is another informed conversation about the existing evidence, rather than a new autism-based reason to change vaccination timing.
A Skeptical Read
A Skeptical Read
The headline number is impressive, but who made it into the database comparison? The selected children needed qualifying visits, an active-patient designation, and linked birth-parent records. Those requirements may produce a group with different access to care and documentation from families whose records are fragmented or whose children receive less consistent follow-up.
Recorded vaccination status is also shaped by what the participating health systems know. A historically documented dose can be counted, but an outside dose that never reaches the record can remain invisible. Recorded autism depends on assessment and coding as well as underlying development.
These are reasons to question representativeness and measurement before treating the result as universally applicable. They do not demonstrate that the main finding is wrong. A fair skeptical reading recognizes the reassuring association and asks how much it depends on the selected population and its patterns of care.
Study Critic
Study Critic
The primary hazard ratio was 0.97, with a 99% confidence interval of 0.91 to 1.03. Under the fitted model, that interval spans a 9% lower to a 3% higher relative diagnosis hazard. These are relative comparisons, not changes of nine or three percentage points in a child’s probability of autism. The interval captures modeled statistical uncertainty, not every possible bias.
The harder questions concern implementation. Reported median follow-up was 853 versus 366 days in the broader vaccinated and unvaccinated groups, and descriptions of the start of follow-up differ. The landmark comparator’s handling of later vaccination needs clarification. Those details matter when groups must be compared over equivalent stretches of time.
The area-deprivation missingness figures also disagree, and the diagram includes sex while the main adjustment list does not. These are specific reporting issues requiring clarification; the available main text does not establish exactly how the underlying code handled them.
Compared to Past Research
Compared to Past Research
This paper adds a large US electronic-record cohort to an existing body of research. Its main result points in the same direction as Hviid and colleagues’ Danish cohort of 657,461 children, which reported an adjusted hazard ratio of 0.93 with a 95% confidence interval of 0.85 to 1.02. The populations, record systems, and uncertainty levels differ, so the two estimates should not be treated as interchangeable.
Jain and colleagues’ US study considered whether an older sibling had autism, a family-history dimension unavailable in the current paper. It found no increased association with MMR regardless of the older sibling’s autism status. The Cochrane review cited below also found no evidence of an MMR-autism association.
The value of the new study lies in an additional setting and comparison. Confidence comes from considering results across independently conducted studies, including their different strengths and limitations. Its larger sample does not make earlier designs or family-history analyses obsolete.
Practical Considerations
Practical Considerations
For a family, the useful practical distinction is between two tasks: discussing vaccination evidence and understanding a child’s developmental history. This paper can inform the first task. Its coded outcome and retrospective records cannot complete the second.
The lower estimates in two later vaccination windows do not establish an optimal schedule. Children were not randomly assigned to those windows, and their reasons for receiving vaccines at different ages may also relate to care, documentation, or developmental concerns. Turning those estimates into timing instructions would go beyond the comparison.
For health systems, the paper highlights the importance of complete vaccination records and continuing diagnostic follow-up. A missing outside vaccination record or an assessment occurring after a child leaves the system can change what an electronic dataset captures. Those are practical measurement issues raised by this study, rather than evidence that any individual record is necessarily inaccurate.
Future Directions (Expected)
Future Directions (Expected)
A useful next step is a transparent account of how this analysis was implemented. The authors could specify the starting date for each model, show how children vaccinated after a landmark were handled, report each model’s analytic denominator, and reconcile the deprivation-data and adjustment descriptions. These are proposals for clarification, not a claim that a new analysis is already underway.
Further work could examine broader autism spectrum codes, incorporate family history and earlier developmental concerns where records permit, and compare groups with more similar opportunities for diagnostic follow-up. Reporting absolute diagnosis frequencies over a defined, comparable period would also help families interpret the relative estimates.
The aim would be to test how stable the reported association remains under clearer measurement and timing choices. An even larger database alone would not resolve these questions. More transparent comparisons would make the evidence easier to assess and reproduce.
Misreadings & Bad-Faith Takes
Misreadings & Bad-Faith Takes
The primary finding supports no observed increase in recorded childhood autism in this analysis. It does not establish that MMR prevents autism. Neither the 0.97 estimate nor the lower estimates in two later windows justify that preventive claim.
A universal statement about every vaccine outcome would also exceed the paper. The study measured a particular autism diagnosis code and used clinical records with unequal follow-up. Its result belongs alongside the wider evidence, with those boundaries attached.
Criticism can be distorted too. Reporting ambiguities and missing variables do not establish a harmful effect that the study failed to report. They identify questions about confidence and implementation. The declared use of ChatGPT for coding and drafting similarly calls for accountable author review and reproducible methods; it does not by itself determine whether the result is valid.
A faithful public summary keeps the finding and its limits together: an additional reassuring association, with specific methods questions still requiring clarification.
Join the Conversation
Which part of a vaccine study would help you assess it more confidently: the comparison group, the follow-up period, or the way the statistics are explained? Share your question without including private medical details.
Source and supporting literature
Primary source: Read the source PDF on Google Drive. Full supplied main paper, including Tables 1 to 4 and Figures 1 to 5. The linked supplementary appendix was not accessible during this review.
Burstain TL, Jacques D, Burstain JM. Association Between First MMR Vaccination Before Age 2 Years and Childhood Autism in a U.S. EHR Cohort of 2.5 Million Children. Pediatr Infect Dis J. Published online July 28, 2026. doi: 10.1097/INF.0000000000005349. PMID: 42520244.
Hviid A, Hansen JV, Frisch M, Melbye M. Measles, Mumps, Rubella Vaccination and Autism: A Nationwide Cohort Study. Ann Intern Med. 2019;170(8):513-520. doi: 10.7326/M18-2101. PMID: 30831578.
Jain A, Marshall J, Buikema A, Bancroft T, Kelly JP, Newschaffer CJ. Autism Occurrence by MMR Vaccine Status Among US Children With Older Siblings With and Without Autism. JAMA. 2015;313(15):1534-1540. doi: 10.1001/jama.2015.3077. PMID: 25898051. Article and supplement corrected January 12, 2016.
Di Pietrantonj C, Rivetti A, Marchione P, Debalini MG, Demicheli V. Vaccines for measles, mumps, rubella, and varicella in children. Cochrane Database Syst Rev. 2021;11:CD004407. doi: 10.1002/14651858.CD004407.pub5. PMID: 34806766.
Suissa S. Immortal time bias in observational studies of drug effects. Pharmacoepidemiol Drug Saf. 2007;16(3):241-249. doi: 10.1002/pds.1357. PMID: 17252614.
This article distinguishes the authors’ reported findings from this review’s methodological assessment. It provides general evidence interpretation and does not replace an individualized medical or developmental evaluation.
Frequently Asked Questions
Did this study find that MMR vaccination increases autism diagnoses?
No. Its primary adjusted comparison was 0.97, with a 99% confidence interval of 0.91 to 1.03. None of the reported vaccination-age comparisons showed a statistically significant increased hazard of coded childhood autism.
Does 0.97 mean MMR prevents autism?
No. It is an observational estimate slightly below 1, and the primary uncertainty interval includes 1. The lower estimates in two later windows also cannot establish prevention or support delaying vaccination.
Were all 2.5 million children followed until age 8?
No. Age 8 was an upper follow-up boundary. Observation could end earlier at diagnosis, the last recorded encounter, or the study cutoff. Median reported follow-up differed substantially between vaccinated and unvaccinated children.
What does the 99% confidence interval tell us?
Under the fitted model and its assumptions, the primary interval spans a 9% lower to a 3% higher relative diagnosis hazard. It does not describe absolute percentage-point risk, guarantee the absence of bias, or assign a 99% probability to this particular interval containing the true effect.
Did the study examine every form of autism?
No. Its outcome was the encounter diagnosis code F84.0. The authors recommend future analyses using broader autism spectrum codes. Recorded diagnosis timing also differs from the timing of the first developmental differences.
Did the negative-control vaccine prove that confounding was eliminated?
No. The near-null pneumococcal result is a useful check for some shared biases. It cannot exclude every unmeasured factor, MMR-specific vaccination decisions, or biases that offset one another.
What if a parent noticed a change after a vaccine?
That history deserves careful discussion and appropriate evaluation. Temporal order alone does not establish cause. Population studies can assess whether diagnoses are more common after an exposure, but they cannot explain every individual child’s developmental history.
Does this paper support delaying MMR to reduce autism risk?
It provides no evidence of an autism-risk benefit from delaying MMR. The separate age-window comparisons do not establish the best schedule. Questions about vaccination timing or contraindications belong in an individualized discussion using the broader evidence.
Does the paper say anything about cannabis or CBD for autism?
No. It did not evaluate cannabis, CBD, or another autism treatment. Conclusions about MMR cannot be transferred to treatment claims.
How does this compare with previous evidence?
The primary finding agrees with the Danish cohort, the US sibling-history study, and the Cochrane review cited above. Agreement across independently conducted studies is more informative than treating this paper’s sample size as a complete answer by itself.
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