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The Table 2 fallacy is the mistake of reading every coefficient in a multivariable regression model as an effect of that variable on the outcome, when the model was built to estimate the effect of one exposure only. Daniel Westreich and Sander Greenland named it in 2013, after the second table of many epidemiology papers, where adjusted estimates for the exposure and for every covariate are printed side by side from one model. The fix is to report only the estimate the model was designed to identify, or to fit a separate model, with its own adjustment set, for each estimate you want readers to interpret causally.
What is the Table 2 fallacy?
In a typical observational paper, Table 1 describes the study population and Table 2 reports the results of the regression analysis. The habit the fallacy targets is putting the effect estimate for the primary exposure and the estimates for the secondary exposures (confounders, other risk factors, predictors of the outcome) in the same column, from the same model, with the same presentation. In their 2013 paper in the American Journal of Epidemiology, Westreich and Greenland note that this is common, and they suggest a precise distinction between total and direct effect measures from a single model, and the use of multiple models tailored to yield total-effect estimates for covariates (Westreich and Greenland, 2013).
The name is a little unfair to the table itself. Nothing is wrong with printing a table of adjusted estimates. The error lies in the reader’s (or author’s) inference: that because a coefficient came out of a model that adjusts for confounding of the exposure, it must be unconfounded too. It need not be. Each coefficient answers its own causal question, and the adjustment set that suits one question can be wrong for another. This is the same family of reasoning errors covered in the guide to statistical fallacies, but it is a modelling error rather than a logical one, and it differs from the aggregate-to-individual inference described under the ecological fallacy.
Why one model cannot give every coefficient a causal meaning
Consider a model for a binary outcome Y, with a primary exposure X and a covariate Z that you included to control confounding of X. Bandoli and colleagues write the first version in log-risk form as log P(Y=1 | X, Z) = β0 + β1X + β2Z. Under the usual assumptions, β1 is the conditional total effect of X on Y. Now suppose X lies on a pathway from Z to Y (Z causes X, and X causes Y). Then:
- β1 is still the total effect of X, because adjusting for Z removes the confounding of X and Y.
- β2 is not the total effect of Z. Part of Z’s effect travels through X, and because X is in the model, that part is blocked. β2 is a controlled direct effect of Z, with X held fixed.
The DAGitty tutorial on this topic puts the consequence plainly: a controlled direct effect can be stronger, weaker or even of opposite sign to the total effect, and a single regression generally yields at most one interpretable causal coefficient, since estimating the effect of X requires including X while estimating the total effect of Z requires leaving it out (DAGitty: The Table 2 Fallacy). If there is also an unmeasured common cause of Z and Y, the coefficient for Z is a confounded direct effect, which is harder still to interpret. The recommended practice in the tutorial is one regression per causal question, with covariates chosen from the causal diagram for that question: Y ~ X + Z for the effect of X, and a different set for the effect of Z.
Four ways the fallacy misleads
Bandoli and colleagues, writing in Paediatric and Perinatal Epidemiology in 2018, list four distinct problems that arise when the secondary estimates are presented like the primary one (Bandoli et al., 2018). They are easy to conflate, so it helps to separate them:
- False parity of effect types. The primary exposure’s coefficient is a total effect, while a covariate’s coefficient may be a direct effect. Printed side by side, they look like the same kind of quantity.
- The primary exposure as a mediator. If the primary exposure lies on a path from the secondary exposure to the outcome, conditioning on it changes what the secondary coefficient means, and where the mediator and the outcome share an unmeasured cause, it can induce collider stratification bias.
- Unassessed confounding of the secondary exposure. The adjustment set was chosen to deal with confounding of the primary exposure. Nobody checked whether the covariate’s own relationship with the outcome is confounded.
- Functional form. A continuous secondary exposure may be entered linearly with no rigorous consideration of its shape, because the modelling effort went into the primary exposure.
Worked example: preeclampsia and preterm birth
Bandoli and colleagues built a teaching example from California birth data to show the size of the problem. Their cohort began with 3,160,268 live births in California in 2007-2012. They restricted to singletons with gestations of 20-44 weeks (n = 3,067,839) and then to mother-infant pairs with linked hospital discharge records (n = 2,963,888); of those, 102,545 had a diagnosis of preeclampsia and 2,861,343 did not. The cohort-flow counts are in the data table on this page.
The primary exposure was preeclampsia and the outcome was preterm birth. Their Model 1 estimated the risk ratio for preeclampsia while adjusting for previous preterm birth and alcohol abuse (potential confounders) and maternal education (included only as a predictor of preterm birth), and reported all four estimates together. The authors describe Model 1 as the typical Table 2 fallacy. They then re-estimated the secondary exposures properly and reported three changes:
- The estimate for previous preterm birth in Model 1 was a controlled direct effect, because preeclampsia lies on the path from previous preterm birth to preterm birth. When estimated as a total effect it increased by 10%.
- The risk ratio for alcohol abuse was biased by an uncontrolled confounder in Model 1. It fell by 23% once drug abuse was adjusted for.
- The risk ratio for maternal education, which is solely a predictor of the outcome, was essentially unchanged.
The third result matters for how you apply the idea: the fallacy does not mean every covariate estimate is wrong. It means you cannot know without a causal diagram, and that the three covariates in this single table were wrong in three different ways, or not wrong at all. The authors also note that the results were largely unchanged in magnitude when the outcome was restricted to spontaneous preterm birth. They name marginal structural models and g-computation as options when direct and indirect effects are the real target.
How to report adjusted estimates instead
The sources agree on the core practice, and the table below sets out what to do in each situation. It is an editorial summary of the practices in the sources above, not a checklist drawn from a single standard.
| Situation | What to report | Basis |
|---|---|---|
| You want the effect of one exposure | The estimate for that exposure only, from a model whose adjustment set comes from your causal diagram for that exposure | Westreich and Greenland; DAGitty tutorial |
| You also want to say something about a covariate | A separate model for that covariate, with its own adjustment set, labelled as its own analysis | Westreich and Greenland; DAGitty tutorial |
| You need direct and indirect effects of an exposure | An explicit mediation analysis (for example marginal structural models or g-computation), with total and direct effects labelled as such | Bandoli et al. |
| You have a prediction model rather than a causal question | Coefficients as predictors only, with no causal language | Editorial interpretation |
Practical steps for a manuscript:
- State the single causal question and draw the diagram before fitting anything. A short note on confounding variables helps you decide which nodes are confounders and which are mediators.
- Choose the adjustment set from the diagram, not from which variables are available or which change the estimate. Dropping a variable that is really a confounder reintroduces omitted variable bias.
- In the results, show the primary estimate with its interval. If covariate estimates are included in a table for transparency, mark them as not interpreted causally, or move them to a supplement.
- Where a covariate matters in its own right, report the separate model in the methods and say which diagram it came from.
- Name the estimand (total or controlled direct effect) in the text next to every estimate you interpret.
Tools that start from the causal graph, such as the Python library covered in the DoWhy causal inference guide, make step 2 explicit in code, because you must state the graph before an estimate is produced.
Fitting separate models in R and Python
The following is an illustration on simulated data, not a result from any study. The data are generated so that Z affects X, and both Z and X affect Y: X = 0.5Z + noise and Y = 1.0X + 0.8Z + noise. Under that structure the total effect of X is 1.0, the total effect of Z is 0.8 + 0.5 × 1.0 = 1.3, and the controlled direct effect of Z (holding X fixed) is 0.8.
R:
set.seed(42); n <- 1e5; z <- rnorm(n); x <- 0.5*z + rnorm(n); y <- 1.0*x + 0.8*z + rnorm(n)coef(lm(y ~ x + z)) (one model, both coefficients: x is the total effect of X, z is only the direct effect of Z, near 0.8)coef(lm(y ~ x + z))["x"] (the model designed for the effect of X, near 1.0)coef(lm(y ~ z))["z"] (a separate model for the total effect of Z, near 1.3)
Python (statsmodels):
import numpy as np, statsmodels.api as smrng = np.random.default_rng(42); n = 100000z = rng.normal(size=n); x = 0.5*z + rng.normal(size=n); y = 1.0*x + 0.8*z + rng.normal(size=n)both = sm.OLS(y, sm.add_constant(np.column_stack([x, z]))).fit().params (x near 1.0, z near 0.8 which is the direct effect)total_z = sm.OLS(y, sm.add_constant(z)).fit().params[1] (near 1.3, the total effect of Z)
The point of the exercise is the last line in each block: the Z coefficient from the single model (0.8) is not the Z effect from the model fitted for Z (1.3). Real data will add sampling error, and for a binary outcome like preterm birth you would fit a log-binomial, Poisson or logistic model, as covered in the guide to types of regression analysis, with the same logic applying on the log or logit scale.
Common mistakes when applying the idea
- Treating it as a ban on tables of adjusted estimates. The problem is the causal reading of every row, not the table.
- Dropping covariates to avoid the problem. Removing a real confounder to make the table “cleaner” biases the primary estimate.
- Assuming a stable coefficient proves a causal one. In Bandoli’s example the education estimate hardly moved, yet the other two did. Stability for one covariate says nothing about another.
- Using the idea as an excuse to skip the diagram. Every row of advice above depends on a stated causal structure.
Sources
- NIH PubMed Central: Westreich D, Greenland S. The Table 2 Fallacy: Presenting and Interpreting Confounder and Modifier Coefficients. Am J Epidemiol 2013;177(4):292-298, checked 2026-11-17
- NIH PubMed Central: Bandoli G, et al. Revisiting the Table 2 Fallacy: A Motivating Example Examining Preeclampsia and Preterm Birth. Paediatr Perinat Epidemiol 2018, checked 2026-11-17
- DAGitty: The Table 2 Fallacy, checked 2026-11-17
- Wikipedia: Table 2 fallacy (background and further reading), checked 2026-11-17
Data: Cohort flow in the Bandoli et al. Table 2 fallacy example (California births 2007-2012)
Sequential cohort counts from the preeclampsia and preterm birth teaching example in Bandoli et al. (2018), showing how the analytic sample of California live births was reached and how it splits by preeclampsia status. Counts taken from the paper's Methods text and Table 1.
Period covered: 2007-2012. Coverage: California, USA.
| Cohort step | Births (count) | Description |
|---|---|---|
| All live births, California 2007-2012 | 3160268 | Starting population |
| Singletons, gestation 20-44 weeks | 3067839 | First restriction |
| Linked mother-infant hospital discharge records | 2963888 | Analytic cohort |
| Preeclampsia: yes | 102545 | Primary exposure present |
| Preeclampsia: no | 2861343 | Primary exposure absent |
Sources
- Bandoli G, et al. Revisiting the Table 2 Fallacy (PMC6103824) (accessed 2026-11-17)
Compiled by CASRAI from the sources above. Free to reuse under CC BY 4.0 with attribution.







