What is the Table 2 fallacy?

The Table 2 fallacy is presenting every coefficient from a single adjusted regression model as though each were a causal effect estimate. An adjustment set chosen to identify the effect of the exposure is generally the wrong set for any other variable in that model, so the covariate coefficients are not interpretable as effects even when the exposure’s coefficient is.

The name comes from the position such tables usually occupy in a paper. Daniel Westreich and Sander Greenland named the error in “The table 2 fallacy: presenting and interpreting confounder and modifier coefficients” (American Journal of Epidemiology 2013;177(4):292–298), and their abstract states the defect without hedging: presenting exposure and confounder estimates together invites “confusion of direct-effect estimates with total-effect estimates for covariates in the model”, and those covariate estimates “may also be confounded even though the effect estimate for the main exposure is not confounded.”

The three separate defects in one table

The Table 2 fallacy is three distinct failures wearing one name, and a manuscript can commit any one of them alone. Westreich and Greenland set out all three in the 2013 paper, and a reviewer’s objection is only answerable once you know which one you are being accused of.

Estimand type. The exposure coefficient is a conditional total effect. A covariate’s coefficient in the same model is a controlled direct effect with respect to the exposure — the part of that covariate’s effect that does not travel through the exposure. Take a model of stroke risk on some exposure, adjusted for age and smoking status: smoking’s coefficient is the portion of smoking’s effect on stroke that is not mediated by the exposure, which is not what anyone reading a stroke risk-factor table believes they are reading.

Residual confounding. The model contains the exposure’s confounders because someone chose them for the exposure. It does not contain the covariate’s confounders, because nobody was estimating the covariate’s effect when the adjustment set was assembled. A covariate coefficient can therefore be badly confounded in a model whose exposure coefficient is not confounded at all.

Effect heterogeneity. Westreich and Greenland add that interpretation “is further complicated by heterogeneity (variation, modification) of the exposure effect measure across covariate levels.” Where the exposure effect differs by age, a model with no interaction term forces the age coefficient to a single number that describes neither the exposed nor the unexposed. Deriving the sets from a directed acyclic graph makes all three visible before the model is fitted.

How it happens

The fallacy enters through an ordinary and entirely defensible modelling choice. A model regresses the outcome on the exposure, adjusting for age, sex, smoking and comorbidity. The exposure coefficient is what the analyst set out to estimate, and if the adjustment set is right for it, that estimate is valid.

The table then reports coefficients for age, sex, smoking and comorbidity too, and readers — and often the discussion section — interpret them as the effects of those variables. But smoking’s coefficient is adjusted for the exposure, which may be a mediator of smoking’s effect, and is not adjusted for smoking’s own confounders, which were never in the model because nobody was estimating smoking’s effect.

Each variable requires its own adjustment set, and the sets conflict. Conditioning on a mediator rather than a confounder removes part of the covariate’s effect by construction; omitting the covariate’s own confounders leaves the remainder biased by an unknown amount in an unknown direction. The two errors act on the same coefficient at the same time and do not cancel.

Worked example: preeclampsia and preterm birth

Bandoli and colleagues quantified the fallacy on 2,963,888 singleton California births from 2007 to 2012 (Paediatric and Perinatal Epidemiology 2018;32(4):390–397). They fitted a modified Poisson model for the total effect of preeclampsia on preterm birth, adjusting for previous preterm birth, pregnancy alcohol abuse, maternal education and maternal socio-demographic factors — then re-estimated each covariate as its own total effect, with its own adjustment set, and compared.

The three covariates moved by three different amounts. The estimate for previous preterm birth, a controlled direct effect in the original model, rose by 10% when estimated as a total effect. The risk ratio for alcohol abuse, confounded in the original model by an uncontrolled variable, fell by 23% once drug abuse was adjusted for. The estimate for maternal education, which was solely a predictor of the outcome, was essentially unchanged.

That spread is the operational point. The error is not a constant that a reader can mentally subtract, and its size cannot be read off the table: one covariate was wrong by a tenth, one by nearly a quarter, and one was fine. Nothing in the model output distinguishes them. Confidence intervals, model fit statistics and p-values are identical in form for all three rows, which is why the fallacy survives peer review — see reviewer says correlative, not causal.

The published case: OpenSAFELY

Williamson and colleagues reported factors associated with COVID-19-related death using OpenSAFELY (Nature 2020;584(7821):430–436), linking primary care records of 17,278,392 adults to 10,926 COVID-19-related deaths in one adjusted Cox model that reported hazard ratios for a long list of characteristics: male sex at HR 1.59 (95% CI 1.53–1.65), and, compared with people of white ethnicity, Black and South Asian people at HR 1.48 (1.29–1.69) and 1.45 (1.32–1.58).

Westreich, Edwards and van Smeden responded in Epidemiology 2021;32(1):e1–e2 under the title “Comment on Williamson et al. (OpenSAFELY): The Table 2 Fallacy in a Study of COVID-19 Mortality Risk Factors.”

The structural point generalises to any adjusted risk-factor table. An ethnicity coefficient adjusted for comorbidity and deprivation is an estimate with those pathways blocked, so it answers a narrower question than “what is the total mortality difference associated with ethnicity in this population” — the question a policymaker reading the table will assume was answered. Comorbidity and deprivation are plausibly on the causal path, and adjusting for a variable on the path removes exactly the part of the association that a health system might act on. Reporting a direct effect where a total effect was wanted is not a rounding error; it is a different quantity, which is why health equity reporting treats the estimand choice as a substantive claim rather than a modelling detail.

How common the Table 2 fallacy is in published work

The Table 2 fallacy has one published prevalence estimate that counts the fallacy itself in a defined literature. Akinkugbe and colleagues screened 1,358 articles across four oral health journals published between 2013 and 2018, reviewed 421 in full text, and found that 189 of them — 45% — committed the fallacy (Community Dentistry and Oral Epidemiology 2021;49(2):103–109). Their diagnosis of the mechanism is that presenting the estimates on one table “inadvertently encourages the reader to interpret all estimates the same way, often as total effects.”

That is the only prevalence figure this page will stand behind, and it should be quoted as what it is: one scoping review, four journals, one discipline, one six-year window. Whether the rate is similar elsewhere in medicine is a question the published literature has not answered, so do not carry the 45% across into a field it was not measured in.

The editorial response is broader than the evidence base. Editors of 30-plus respiratory, sleep and critical care journals issued joint guidance on confounder control and results reporting in causal inference studies (Lederer et al., Annals of the American Thoracic Society 2019;16(1):22–28). The fallacy has since drawn dedicated commentaries in surgery (Mah et al., Annals of Surgery 2026;284(2):445–447) and in general clinical research (Tay et al., Annals of the Academy of Medicine, Singapore 2026;55(7):383–387), whose closing specification is the one to memorise: “A regression table is not a menu of modifiable risks.”

How to detect it in your own work

Look at whether your results or discussion attribute meaning to any coefficient other than the exposure’s. Phrases like “older age was associated with worse outcome, independent of treatment” are the signature.

Then ask: was the model built to estimate that variable’s effect? If not, the coefficient is a nuisance parameter that helped identify the exposure effect, and nothing more.

Six further tells find most remaining instances:

• A table captioned “risk factors for” or “predictors of” that reports one model. The caption promises several effects; the model delivers one.
• The words “independent predictor” or “independently associated with” applied to a covariate. Independent of what, and adjusted for whose confounders, is never stated because it cannot be.
• One justification sentence covering twelve adjustment variables. A DAG-derived set for the exposure is not a DAG-derived set for anything else.
• Interaction terms read causally. Tay and colleagues show that the same error arises when interaction terms are interpreted as causal. An interaction coefficient is scale-dependent besides: the same data can show modification on the multiplicative scale and none on the additive scale.
• Coefficients from a propensity score model quoted as effects. That model exists to predict treatment; its coefficients were never intended to be causal, and the design does not identify them.
• A Cox model treated as if its covariate rows were comparable to a marginal analysis. The hazard ratio is non-collapsible, so a covariate’s adjusted hazard ratio differs from its unadjusted hazard ratio even when there is no confounding at all.

A prediction model is a separate case with a stricter rule: none of its coefficients are effects, including the one you care about, because the model was fitted to minimise error rather than to identify anything. Interpreting a coefficient from a model that was tuned for out-of-sample accuracy conflates two goals — see overfitting.

What to do instead

Report the exposure coefficient as the estimate of interest and present covariate coefficients as adjustment terms, explicitly labelled as not interpretable as effects — or omit them.

If a covariate’s effect genuinely interests you, fit a separate model with an adjustment set chosen for that variable, and say you have done so.

Four practices make that routine rather than an act of virtue:

Write the estimand before the model. Name the exposure, the outcome, the population and the contrast in one sentence in the methods. A model without a written estimand invites every coefficient to be read as one.

Derive the adjustment set from a stated causal structure. A DAG, or an explicit list of assumed relationships, converts “we adjusted for potential confounders” into a set that can be checked, and makes it obvious that a second variable needs a second set.

Fit one model per question and say how many you fitted. Bandoli and colleagues needed four models for four questions. Reporting several models is not p-hacking when each was pre-specified to answer a different, named question and all are reported.

Label the estimand type on every row you keep. Westreich and Greenland’s own remedies are a precise distinction between total and direct effect measures within a single model, and the use of multiple models tailored to yield total-effect estimates for covariates. Where a row survives, mark it as a total effect or a controlled direct effect. A column header reading “adjustment term — not an effect estimate” takes one line and removes the ambiguity permanently.

When the obvious remedy is unavailable

Fitting a separate model per covariate is the textbook remedy and is often impossible, and four common obstructions each have a specific fallback that is not silence.

You genuinely need to rank many predictors. Descriptive epidemiology sometimes has no single exposure. Dharma, Fu and Chaiton argue that a multivariable coefficient table is the wrong instrument for that goal and propose machine learning instead — nested cross-validation for tuning, variable importance scores for ranking, and partial dependence plots to display each important variable’s association with the outcome (International Journal of Environmental Research and Public Health 2023;20(13):6194). The output is explicitly descriptive, which is the honest label.

The covariate’s confounders were never measured. Fitting a second model does not help when the data lack what that model needs. Name the covariate, name the missing confounder, and state the direction the omission would push the estimate. That is a data-collection limitation with a stated sign, which is a far stronger limitations section than “residual confounding cannot be excluded”.

The journal template requires a full multivariable table. Keep the table and change its semantics. Retitle the covariate column as adjustment terms, footnote the estimand for the exposure row, and state in the results text that covariate coefficients are reported for transparency of model specification and are not effect estimates.

The sample is too small for multiple models. State which single coefficient is the estimand and decline the rest in the text, explicitly. Declining is a finding about the design, not a failure to analyse.

When it is not the Table 2 fallacy

Reporting a covariate coefficient is not the fallacy; interpreting it as an effect is. A table that prints adjustment terms under a header saying they are adjustment terms, with a discussion that mentions only the exposure, has committed nothing.

Three neighbouring problems are routinely confused with it, and naming the right one changes the fix. Multiple testing concerns error rates across many tests and is repaired by a multiple testing correction; the Table 2 fallacy survives any correction, because the coefficients are not estimating the intended quantity however their p-values are adjusted. Simpson’s paradox is a reversal between aggregated and stratified associations, a property of the data rather than of what a coefficient is asked to mean. Selection bias originates in who entered the analysis and is untouched by covariate choice, whereas the Table 2 fallacy is entirely a question of which variables were adjusted for and why.

One further case is genuinely benign, and only the second model proves it. A covariate that is solely a predictor of the outcome, with no causal relationship to the exposure and no confounders of its own inside the analysis, can have a coefficient that coincides with its total effect — maternal education behaved that way in Bandoli’s cohort, changing essentially not at all. You cannot identify that case by inspecting the table.

What a reviewer will say

A reviewer will say that secondary coefficients are being over-interpreted, that the adjustment set is not valid for the covariates, or that the discussion draws conclusions the model does not support.

The specific sentences recur, and they are the ones that decide papers. “The adjustment set was selected to identify the effect of the exposure; the coefficients for age and comorbidity are not interpretable as effects of those variables.” “Table 2 is presented as a table of risk factors, but only one estimand is identified by this model.” “The abstract states that diabetes was an independent predictor of the outcome; the model does not adjust for confounders of diabetes.” “The coefficient for smoking is adjusted for the exposure, which the authors’ own introduction describes as a downstream consequence of smoking.” “Please state the estimand for each row retained in Table 2.” “The discussion recommends targeting a covariate that the analysis was not designed to estimate.”

Anticipating the objection in a limitations paragraph does not resolve it. A sentence conceding that “coefficients for covariates should be interpreted with caution” attracts the follow-up that caution is not an estimand — a pattern the causal language check exists to catch before submission.

How to report it

Report the analysis by naming the estimand first, the exposure second, and the type of every coefficient you retain third. STROBE item 16(a) asks authors to “Give unadjusted estimates and, if applicable, confounder-adjusted estimates and their precision (eg, 95% confidence interval)” and to “Make clear which confounders were adjusted for and why they were included” — a request for the reasoning behind the adjustment set, not for the adjustment set’s coefficients.

State the exposure, the outcome and the contrast in the methods. Give the causal structure that produced the adjustment set. Report the exposure estimate with its confidence interval in the primary table. Put the adjustment variables in a footnote, or in a column headed as adjustment terms. Where a covariate estimate is reported deliberately, say which model produced it, which set it was adjusted for, and whether it is a total or a controlled direct effect. In the discussion, make claims about the exposure only, unless a second named model supports the second claim.

Related

Confounding · Mediator versus confounder · Collider bias · Directed acyclic graphs · Epidemiology review

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Frequently asked questions

What does the Table 2 fallacy mean in research?

The Table 2 fallacy means reading a multivariable regression table as a list of causal effects when the model identifies only one. The adjustment set was chosen for the exposure, so it typically omits each covariate’s own confounders and includes its mediators, and the covariate coefficients answer no well-defined causal question.

Why can’t I interpret every coefficient in my regression model?

Because the adjustment set was chosen to identify one effect. For any other variable, that set will typically omit its confounders and include its mediators, so its coefficient answers no well-defined causal question. Westreich and Greenland describe the result as confusion of direct-effect estimates with total-effect estimates for covariates in the model.

Can you give an example of the Table 2 fallacy?

Bandoli and colleagues re-estimated three covariates from a preeclampsia and preterm birth model across 2,963,888 California births. The estimate for previous preterm birth rose 10% when refitted as a total effect, the alcohol abuse risk ratio fell 23% once drug abuse was adjusted for, and maternal education barely moved — three rows of one table, three different errors.

How do you avoid the Table 2 fallacy?

Either remove covariate coefficients or label them explicitly as adjustment terms that are not effect estimates. Editors of more than 30 respiratory, sleep and critical care journals have issued joint guidance on confounder control and results reporting, so in some fields the expectation is already written down. Write the estimand before fitting, and derive the adjustment set from a stated causal structure.

Can you estimate several effects from one dataset without committing the Table 2 fallacy?

Yes, with a separate model and a separate adjustment set for each. What you cannot do is read several effects off one model. Report how many models you fitted and which question each was pre-specified to answer.

Is the Table 2 fallacy the same as multiple testing?

No. Multiple testing concerns error rates across many tests. The Table 2 fallacy is about identification: the coefficients are not estimating what they appear to estimate, regardless of how many are reported, and no correction to their p-values changes what they estimate.

Where does the name “Table 2 fallacy” come from?

The name comes from the position such tables usually occupy in a paper, and was coined by Daniel Westreich and Sander Greenland in the American Journal of Epidemiology in 2013 (177(4):292–298). Table 1 conventionally describes the sample; Table 2 conventionally carries the adjusted model whose rows readers then mistake for a list of effects.