What "Adjusted for Age, Sex and BMI" Actually Did — How to Read Confounding and Adjustment

You have probably seen this single line attached to a paper's results: Adjusted for age, sex, and BMI. Adjustment is the work of aligning calculations as if comparing people with the same age, sex, and body mass index. This line is usually read to mean, "Since the other conditions were matched identically, what remains is the true effect."

Let us look at what actually happens through a single case. The question is how much preeclampsia (a disease where blood pressure rises during pregnancy) causes preterm birth. The data is 2,963,888 birth records of singleton babies born in California from 2007 to 2012 (PMID 29782045). The researchers set up a regression model. A regression model is an equation that puts in multiple variables (characteristics whose values differ from person to person, such as age and education) all at once, and calculates how much each variable is related to the outcome. Into this model, they put preeclampsia along with background factors of the mother, such as prior preterm birth, alcohol abuse during pregnancy, maternal education, income, and residence.

Up to this point, it is a common picture. When you run the model, a table comes out. Below the line for preeclampsia, the lines for prior preterm birth, alcohol abuse, and education line up side by side, and coefficients are written for each line. A coefficient is a number representing the magnitude of the relationship between that variable and the outcome, and in this study, it was written as a risk ratio, which is the ratio of event rates between the group with that characteristic and the group without it. This study calculated separately what those lines were each measuring. The value for prior preterm birth grew by 10%, the value for alcohol abuse shrank by 23%, and the value for maternal education barely changed.

This means that three numbers that looked identical while listed side by side in the same table were, in fact, three different kinds of quantities.

The takeaway of this article is a single sentence. The phrase "adjusted for" is a claim about where you placed that variable in the causal structure. A causal structure is a relationship map connecting which variables affect which other variables. Adjustment is easily read as a report that something has been cleanly wiped away, but if you pick the wrong spot, adjustment creates problems instead of fixing them.

There are six new terms you will learn in this article, and each term is defined where it first appears.

⚠️ The diseases, drugs, and policies appearing below are all examples just to show how to read numbers. They are not judgments on which treatments are good or bad, and each number has meaning only within that study's design, subjects, and time point.

Why You Need to Know — The Counted Facts

The root of this problem is confounding. Confounding is when an apparent link between things is actually caused by another factor that affects both the suspected cause and the outcome (covered in "If People Who Take It Live Longer, How Were They Different to Begin With? — Confounding"). Several surveys have counted how papers handle confounding, and the results fall broadly into three groups. The numbers below apply to the specific sets of papers chosen by each survey, and cannot be directly transferred to "papers in general."

① Even when confounding is mentioned, papers rarely go as far as "read this with caution." The subjects were 120 randomly selected studies published in 2011–2012 in general medical, epidemiology, and specialty journals with the highest impact factors (PMID 28943377). All were observational studies—meaning the researchers did not assign treatments or lifestyles, but simply watched what had already happened to people. They were a mix of cohort studies, which follow people over time and count events, and case-control studies, which gather people with and without a disease and compare their pasts backward.

Not a few papers brought up confounding. Mentioning confounding in the abstract or discussion was done by 68 papers (56.7%), hinting at it indirectly by 20 papers (16.7%), and neither mentioning nor hinting at it by 32 papers (26.7%). However, only 2 papers (1.7%) wrote that the results should be read "with caution" because of confounding. Only 4 papers (3.3%) included limitations related to confounding or other biases in their conclusion sections.

The authors summarize it thus: even when mentioning confounding, authors are usually confident that it has little to do with their own results, and rarely ask for cautious interpretation. Therefore, the mere presence of the word "confounding" in a limitations section does not mean the author is telling you to read the results with care. There is also an incidental result. Papers that noted their results might have been affected by confounding were actually cited more often than those stating they were likely unaffected (median of 6.3 vs. 4.0 citations per year, P = 0.04). The authors noted this as meaning that more cautious admissions do not carry a penalty in citations (PMID 28943377).

The picture was similar among 160 inflammatory bowel disease observational studies (PMID 33296517). Most actually used strategies to reduce confounding or bias (139 papers, 86.9%). Many papers also admitted at least one unadjusted confounding factor (116 papers, 72.5%). Yet only 60 papers (37.5%) commented on whether this might have affected the main results, and only 7 papers (4.4%) requested a cautious interpretation. In this survey as well, there was a positive association where papers mentioning confounding were cited more, but requesting cautious interpretation was not.

② Every row of an adjusted table is read as a risk factor. A risk factor is something that increases the likelihood of developing a disease or event. Translated to our previous birth record table, this means reading not just pre-eclampsia, but every other row listed alongside it, as the effect of that specific variable. This reading is an error we will name later, and it appeared in 67% (129) of 193 orthopedic studies (PMID 33933587). The subjects were studies published in 2019 across seven highly cited orthopedic journals that presented results from models putting multiple variables together in a table. The basis for choosing variables was also weak. Only 16% (31 papers) selected variables by reasoning about which variable causes what, while 35% (67 papers) chose variables using statistical methods.

The dental public health field is similar. Among 421 observational studies published between 2013 and 2018 across 4 dental public health journals, 189 (45%) showed the same problem (PMID 33368566). The authors describe the mechanism like this: putting multiple estimates from a single model into the same table encourages readers to read all those values in the same way, often as measuring the entire share of that variable.

③ Multiple risk factors are all stuffed into a single model. Among 162 cohort and case-control studies dealing with multiple risk factors for cardiovascular disease, diabetes, and dementia, over 70% of the studies put all risk factors into a single model and adjusted them against each other (PMID 40038753; published between January 2018 and March 2023). The recommended method is to adjust each individual risk factor separately for its own confounding factors. Doing so was done by 10 papers (6.2%), all of which were studies targeting specific risk factors. The authors conclude that this practice can lead to bias from overadjustment and misleading estimates, and urge us not to indiscriminately throw risk factors into a single model.

The Big Picture — There Are Three Positions That Determine Whether to Adjust

Here, exposure is the candidate cause (a drug, habit, or disease) and outcome is the event we are trying to measure (disease onset, death, or readmission). When there is a third variable in addition to the exposure and outcome, its position is determined by how it is connected to both. There are three positions that determine whether to adjust. Whether you must adjust or must not adjust depends on the position.

A confounding variable is a common cause that affects both the exposure and the outcome. This is the other factor that causes confounding, as mentioned earlier. In summer, more ice cream is sold and water recreation accidents also increase. What increases both together is the heat, and ice cream does not cause accidents. If you set ice cream as the exposure and accidents as the outcome, the heat is a confounding variable. You must adjust for such variables. If you compare only days with the same heat, the apparent association disappears.

A mediator is a variable on the pathway through which the exposure affects the outcome. Let us say that exercising reduces body weight, and reduced body weight lowers blood pressure. Body weight is the stepping stone between exercise and blood pressure. If you want to know the entire effect of exercise on blood pressure but adjust for body weight, the share that passes through body weight is cut out entirely. What remains is only "the share that went down without passing through body weight." Therefore, to see the full effect, you must not adjust for a mediator.

A collider is a variable that is affected by both the exposure and the outcome. The name comes from the fact that it is a place where two arrows come and collide. Let us think of restaurants. They survive if the food is delicious or the location is good, and they close if neither is true. When you gather only the surviving restaurants, a relationship that did not exist appears between taste and location. This is because if a restaurant survived despite poor taste, it means the location was good. Here, "survived" is a collider. Looking only at what survived is placing a condition on that variable, and putting that variable into the model to adjust for it is also placing a condition on it. Placing a condition on a collider creates an association that was not there. (Ice cream, exercise, and restaurants are examples we made up for explanation.)

There are also variables that belong to none of the three positions. Variables that affect only the outcome regardless of the exposure are like that. Maternal education, which will appear later, is such a case.

⚠️ The three positions cannot be distinguished just by looking at the data. Whether a variable comes before the exposure, on the pathway, or below it comes from outside the data—specifically, from the knowledge the researcher holds. Therefore, choosing which variables to include is a claim about causal structure and cannot be replaced by statistical procedures alone.

Turning that claim into a picture is a causal diagram. A causal diagram is a drawing where variables are laid out and arrows show what affects what. Transferring the assumptions about confounding variables, mediators, and colliders to this picture helps in choosing variables to adjust for and avoiding common sources of bias and confounding (PMID 40707288). The authors of that primer view this framework even as a supplement or alternative to large-scale randomized trials. However, this picture provides scientific backing only for part of the variable selection phase (PMID 36328854). The same review shows using Framingham Heart Study data how severely wrong effect estimates are calculated if variables are put into the model ignoring their types and causal order.

Drawing the picture does not solve everything either. In one theoretical case, standard causal diagrams failed to fully identify confounding and bias, and yielded a flawed set of adjustment variables (PMID 35612081). The ones who made this comparison are the authors of the tool themselves, who also write that additional research is needed to make the tool more usable. In fact, studies that actually draw the picture are rare. Among the 31 papers that selected variables using Causal Inference in the preceding orthopedic survey, 3 drew this picture (PMID 33933587).

The reason all this worry is necessary in observational studies is that there is no randomization. Randomization leaves it to chance, like drawing lots, who goes into which arm. Drawing lots distributes even differences the researcher didn't think of fairly evenly to both sides. Observational studies lack that mechanism, so the researcher must decide which variable to place in which position. The lottery example was covered in "If People Who Take It Live Longer, How Were They Different to Begin With? — Confounding".

Basic Principle — What "Adjusted For" Actually Does

Adjustment is a calculation performed on data that have already been gathered. Putting a variable into a model means comparing people who share the same value for that variable. Whether this comparison yields a causal effect—that is, the portion by which the exposure genuinely altered the outcome—comes not from the data, but from assumptions. Those assumptions break down in several ways, and this article looks at two of the most common spots. We also look at one study that actually measured the size of what remains after the break.

① What Is Not Measured Cannot Be Matched — Unmeasured Confounding

Unmeasured confounding is when a confounding variable is not measured at all, making it impossible to even put into the model. If hospital records do not contain smoking status, there is no way to adjust for smoking. This seems obvious, but the problem is its magnitude.

That magnitude can be measured through simulation (PMID 17615092). A simulation is a method where a computer builds fake data with pre-determined correct answers, letting you see what an analysis produces. This study built data such that in reality, the exposure had no causal effect whatsoever on the outcome. The exposure was made to follow a normal distribution (a bell-shaped distribution with a high middle), and two or four confounding variables of the same shape were included. The authors then calculated how large the apparent association could become. When the confounding variables were uncorrelated with each other, greater residual and unmeasured confounding led to greater bias; when they were correlated, the pattern was more complex.

The authors' conclusion is that under plausible assumptions, effect sizes commonly reported in observational epidemiology studies can be produced by residual or unmeasured confounding alone. If an association is of the size commonly seen in papers, that magnitude alone cannot distinguish whether it is a true effect or generated by confounding.

② What Is Measured Poorly Cannot Be Matched Either — Residual Confounding

Residual confounding is when a confounding variable is included, but measured so coarsely or poorly that the confounding is not fully removed and remains. If smoking is measured only as "yes/no," smoking one cigarette a day and two packs a day end up in the same bucket.

The direction of the bias left this way is also hard to guess (PMID 17615092). Measurement error on the exposure side is a different story. If error arising while measuring the exposure occurs independently of the outcome, it is well known that under certain conditions, the bias moves toward the null value—that is, "no effect." Measurement error in a confounding variable leads to residual confounding, and it is not clear which direction that bias will point. In other words, the phrase "we adjusted for it" carries the additional claim that the variable was measured accurately.

So What Remains After Adjustment?

The magnitude of the bias remaining after adjustment is usually unknown. That is because there is no correct answer to check it against. In one US state's Medicaid (public health insurance for low-income populations), that correct answer materialized (PMID 34978862). More than two-thirds of the enrollees in a given region were randomly assigned to one of five insurance plans. This situation, where a system acts as a lottery instead of researchers, is called a natural experiment. Among 137,933 enrollees in 2013–2014, 31.1% chose their plan themselves, and 68.9% were randomly assigned. Because people who were randomly assigned and people who chose for themselves existed together within the same data, the magnitude of what remained after adjustment could actually be measured. As expected, clear differences in enrollee characteristics across plans were found only in the self-selected group.

Spending scores indicate how much higher or lower a given plan's spending is compared to the average plan. When the spending scores of the same plans were calculated separately in the two populations, they differed by $67 per average enrollee (in absolute value, 95% confidence interval $38–$123). A confidence interval is the range where the true value is likely to lie. This difference amounted to 4.2% of average spending per enrollee, and was difficult to dismiss as mere sample chance (P = 0.009). The procedure to adjust for differences in patient mix is called risk adjustment. Even when risk adjustment was applied, the difference shrank only slightly to $62 (P = 0.012). Further adjusting for social factors did not substantially change the estimate either. Residual confounding was similarly substantial for most other performance metrics. The authors' conclusion is that because residual confounding can be substantial in risk-adjusted performance evaluations, policymakers should not assume that risk adjustment isolates differences in true plan performance. As a limitation, the possibility of heterogeneity in plan effects between the two populations was noted (PMID 34978862).

The fact that the bar heights before and after adjustment are nearly identical means that risk adjustment stripped away only a fraction of the bias originating from enrollee composition.

⭐Table 2 fallacy — The mistake of reading the adjustment variable's row as an effect

Let us return to the California birth record study that opened this article. The model was built to estimate the total share of preeclampsia's effect on premature birth—in other words, the sum of all differences caused by preeclampsia, regardless of the pathway they took through. The coefficients included together in that model were each of the following.

• The coefficient for previous premature birth was the share seen while holding other variables in the model fixed. Because it was a value missing the share passing through those variables, it grew by 10% when re-estimated for the total share of previous premature birth.
• The risk ratio for alcohol abuse was skewed due to confounding variables that were not put into the model. It shrank by 23% when substance abuse was adjusted for.
• The risk ratio for maternal education barely changed because it was a variable that only predicted the outcome and did not belong in any of the three places.

The authors' conclusion is that reporting multiple effect estimates from a single model together can lead to misunderstandings and a lack of reproducibility, so one must carefully consider the types of effects that a statistical model estimates (PMID 29782045).

This trap has a name. The Table 2 fallacy refers to the practice of including the estimates of the exposure of interest and the adjustment variables from a single model together in the same table, and was named in 2013 (PMID 33368566). The danger lies in the reading that the table invites—namely, making people read every row as the same kind of value.

The paper that gave it that name lists three problems (PMID 23371353). First, it establishes a term. A covariate is a variable put into the model not because it is the target of interest, but to strip away its influence—in other words, an adjustment variable. First, it makes people confuse the share seen while holding that variable fixed with the total share of that variable for a covariate. The previous premature birth row above is such a case. Second, even if the estimate of the main exposure is not confounded, the estimate of the covariate may be confounded. The alcohol abuse row is such a case. Third, interpretation becomes more complex due to heterogeneity, where the effect of the exposure varies depending on the value of the covariate. The suggestion is to write down precisely what kind of value each of the numbers from a single model is, and to use a separate model for it if the total share of the covariate is needed.

Rows of adjustment variables are often read as independent risk factors (PMID 42531045). This is because even a model built to estimate the effect of a single exposure outputs coefficients for adjustment variables like age, sex, comorbidities, and lifestyle together. This is the case even though that analysis was not designed in the first place to estimate the effects of those variables. A 2026 commentary nails it down like this: Using adjustment is not the problem. The problem is interpreting each adjustment term as if it were a separate causal estimate. The recommendations are four. State precisely what value the analysis aims to measure and what the exposure is. Choose adjustment variables from a hypothesized causal structure. Interpret only the exposure's coefficient. Fit a separate model for each additional question. And the final two sentences are this section's summary: A regression table is not a menu of modifiable risks. An association is clinically actionable only when the study is designed to support that interpretation (PMID 42531045).

The same trap appears in research on socioeconomic status (social standing measured by education, occupation, and income) under the name "mutual adjustment fallacy" (PMID 30606167). It is the practice of putting education, occupation, and income into a single model to mutually adjust for them, and then reading each coefficient equally as the "independent" effect of that indicator. Let us assume that education leads to occupation, and that education and occupation together determine income. Then the coefficient for education represents only the share that does not pass through occupation or income, and the coefficient for income represents the share with the confounding of education and occupation stripped away. The three coefficients are different quantities, each with a different pathway subtracted. Placing the three side by side and comparing them is not comparing like with like. However, this paper also writes down the opposite half. Depending on the situation, adjusting for more distant indicators (education, occupation) may be sufficient to block unmeasured socioeconomic confounding. Then the causal confidence in the adjusted estimate of the closer indicator (income) may actually increase.

There are also studies where what matters among multiple predictors is truly what is important. Research of this kind, where description rather than uncovering causes is the goal, lacked the right methodology, and that frequently led to this error (PMID 37444042). The same paper proposes a five-step machine learning framework as an alternative, and discusses its strengths and weaknesses together.

Common Misconceptions

① "We Adjusted for It, So It's Causal"

To get a causal effect from adjustment alone, you must measure all the variables that need to be accounted for, measure them properly, and pick only the ones that sit in a place where adjusting for them is legitimate. If something unmeasured is left out, it breaks; if a measured thing is measured crudely, it breaks—and that alone can create effects of the magnitude commonly reported in observational epidemiology (PMID 17615092). In natural experiments compared side-by-side with randomization, risk adjustment reduced residual confounding by only a small amount (PMID 34978862). Bias and confounding are common potential explanations for why a statistically significant association appears even when the true relationship is not causal (PMID 28817531).

Still, there are ways to talk about causality in observational studies. JAMA and many other medical journals have restricted causal language to the reporting of randomized trials. A 2024 paper that reexamined this practice leaves intact the point that well-conducted randomized clinical trials are the preferred method for answering causal questions. Building on that, it notes that as observational study methodology advances, when strong assumptions hold, a causal interpretation of well-conducted observational study results can be possible. For some questions, observational studies are practically the sole source of information, can handle populations and settings that reflect actual clinical practice, and can be used to find interventions to test in subsequent experiments. The proposal is a framework of six core questions (PMID 38722735).

② "The More Variables You Put In, the Safer It Is"

The exact opposite can be true. Putting in a mediator carves away the piece along the path, and putting in a collider creates an association where none existed. Such occurrences were not rare. Of 162 studies addressing multiple risk factors, 10 (6.2%) used recommended methods, and over 70% of the studies put all risk factors into a single model to mutually adjust for them (PMID 40038753). A survey of 193 orthopaedic journals showed that 35% (67 papers) selected variables using statistical methods (PMID 33933587).

What needs to be put in are confounders. Confounders are variables that, like any other covariates, must be found, measured, and adjusted for (PMID 38524951).

The recommended direction is to select variables from an assumed causal structure (PMID 42531045).

③ "It's Safe Because We Wrote 'Association'"

It is common for papers to have a practical goal of causality while using only the language of association in their text (PMID 34535799). This is a study that randomly selected 100 papers from top general epidemiology journals between 2014 and 2018 to see whether their goals, analytical methods, and interpretations meshed with one another (were aligned). Explicitly staking a causal claim was done by 13 papers (13%), while 71 papers (69%) framed things in the language of association but practically targeted causality.

All three were completely aligned in 9 papers (9%). Those that explicitly professed causality were aligned more often (5 out of 13, 38%, versus 3 out of 71, 4%). Misalignments were also common. Mismatches between goals and methods occurred in 34 out of 103 judgments (33%), and mismatches between goals and interpretations occurred in 32 papers (31%). However, the most common judgment when comparing goals and methods was "insufficient reporting of methods to judge" (47 papers, 46%). And mismatches between goals and interpretations appeared less often in studies where the methods were aligned (2 papers, 2%, versus 13 papers, 13%).

One commentary directly criticizes this practice (PMID 29565659). Its diagnosis is that authors and editors are reluctant to state the causal goals of their study and call causal effect estimates association estimates. Building on that, this commentary argues that using the word "causality" is necessary to raise the quality of observational studies. It states that clearly revealing causal goals reduces the ambiguity of scientific questions, errors in data analysis, and overstatements in the interpretation of results.

To Go Deeper

What this article established are the names of three positions, and what adjustment does and cannot do. Two other pieces take charge of the two topics that stand on top of that foundation.

• What happens if you adjust for something you must not adjust for — cases where adjusting for mediators reversed the direction of the answer, cases where conditioning on a collider created an association that wasn't there, and studies that put the brakes on the claim that "collider bias explains that paradox." This is the share of "The Variables You Must Not Adjust For — Some Covariates Change the Answer the Moment You Add Them".
• How to measure what is left after adjustment — E-values, negative controls, confounding by indication, propensity scores, and covariate adjustment done even in randomized trials. This is the share of "What Is Left After Adjustment — What E-values, Negative Controls and Propensity Scores Do and Do Not Do".

To go one step further within the scope of this article, it is good to start by looking at a map that illustrates by type which biases frequently arise in which study designs (PMID 32133725). The remaining reading materials are grouped by category in the evidence papers below.

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What this article intends to leave behind is a single reading rule. When you encounter the sentence "we adjusted for," you ask which position that variable occupies. You do not just look at the list of what was adjusted for and move on. The positions that determine whether adjustment is correct were three. If it is a common cause preceding the exposure, adjustment is right; if it is between the exposure and the outcome, adjustment alters the answer; and if it is a variable affected by both the exposure and the outcome, adjustment creates an answer that wasn't there.

And the coefficients of the other rows listed side by side in the table—namely, age, sex, and body mass index—are not the answer to the question that study was trying to answer.

If this rule reads as "do not trust observational studies," this article has failed. The reader's job is one. It is to check whether the paper tells you which variable was placed in which position, and why. If it does not tell you, what that adjustment did is still unknown.

Source Papers

Fact-Checking the Counts

• "Interpretation of epidemiologic studies … consideration of confounding." (2018) — PMID 28943377 — 120 high-impact journal cohorts and case-control studies (2011–12). Confounding mentioned in 68 (56.7%). "Cautiously" in 2 (1.7%), limitations in the conclusion in 4 (3.3%). Papers acknowledging the effect were actually cited more (median 6.3 vs. 4.0 citations per year, P = 0.04).
• "Confounding and bias in observational studies in IBD…" (2021) — PMID 33296517 — 160 observational studies. Confounding mentioned in 67 (41.9%), mitigation strategies in 139 (86.9%), unadjusted confounding acknowledged in 116 (72.5%), commentary on impact on results in 60 (37.5%), call for cautious interpretation in 7 (4.4%). Mention of confounding positively associated with citation count (P = 0.010), call for cautious interpretation not. Reporting is especially poor in case-control studies, non-routine collection, laboratory assessments, and immutable exposures.
• "Multivariable models in orthopaedic research…" (2021) — PMID 33933587 — 193 papers from the top 7 orthopaedic journals by IF in 2019. Table 2 fallacy in 67% (129 papers), causal inference-based variable selection in 16% (31 papers, including 3 diagrams), statistical methods in 35% (67 papers). Authors conclude that reducing these issues appears to require more statistical training and knowledge.
• "A scoping review of Table 2 fallacy in the oral health literature." (2021) — PMID 33368566 — 189 out of 421 papers (45%) across 4 oral health journals. Name coined in 2013. The problem is that it encourages readers to read all values the same way, often as the total share of that variable.
• "Confounder adjustment … multiple risk factors…" (2025) — PMID 40038753 — 162 cardiovascular, diabetes, and dementia multi-risk factor studies (2018–23). Recommended methods in 10 (6.2%), all studies targeting specific factors. Mutual adjustment exceeded 70%. Conclusion to avoid indiscriminate bulk entry.
• "Is the Way Forward to Step Back?…" (2022) — PMID 34535799 — 100 top general epidemiology journals (2014–18). Explicit causal 13 papers (13%) and association language 71 papers (69%), fully aligned 9 papers (9%). Aim-method 34/103 (33%), aim-interpretation 32 papers (31%), unclassifiable 47 papers (46%). Aim-interpretation mismatch is less when methods are aligned (2% vs. 13%).

Concepts and Terms

• "Confounding by Indication, Confounding Variables, Covariates…" (2024) — PMID 38524951 — Independent variable ⊃ Covariate ⊃ Confounder. Covariates are included not because they are of interest, but to strip away their influence.
• "Bias, Confounding, and Interaction…" (2017) — PMID 28817531 — Overview. Why confounding is mostly not a problem in randomly divided groups, why ignoring it in observational studies frequently distorts findings, and how bias and confounding are common potential explanations for a significant association.
• "Where to look for the most frequent biases?" (2020) — PMID 32133725 — A map of selection bias and information bias by type. Which designs each bias arises in most frequently and how to prevent it.
• "The C-Word: Scientific Euphemisms Do Not Improve Causal Inference…" (2018) — PMID 29565659 — A commentary arguing that using the word "causal" is necessary to improve the quality of observational studies. Vagueness of questions, analysis errors, and over-interpretation are reduced.
• "Causal Inference About the Effects of Interventions From Observational Studies…" (2024) — PMID 38722735 — Proceeding from the premise that well-performed randomized trials remain the preferred method, it suggests that causal interpretation of observational studies can be possible when strong assumptions hold. A framework of six core questions.

Causal Diagrams

• "DAGs for dummies: how to extract causation from correlation." (2025) — PMID 40707288 — Primer. It draws assumptions about confounders, mediators, and colliders to help choose variables to adjust for. The authors view this framework as a complement or alternative to large randomized trials.
• "Using Causal Diagrams for Biomedical Research." (2023) — PMID 36328854 — Used in both observational studies and clinical trials, providing scientific rationale for some aspects of variable selection. Examples of miscalculation using Framingham data.
• "OntoBioStat: Supporting Causal Diagram Design and Analysis." (2022) — PMID 35612081 — Standard causal diagrams alone may not fully identify confounding and bias, leading to incorrect covariate sets (theoretical cases). The authors note that the tool requires further research.

Table 2 fallacy

• "The table 2 fallacy…" (2013) — PMID 23371353 — Original source. Confusing direct and total effects of covariates, covariate estimates can be confounded even when the main exposure is not, heterogeneity. The proposal is separating types and using separate models.
• "Interpreting multivariable regression coefficients …: The Table 2 fallacy." (2026) — PMID 42531045 — The problem is not the adjustment, but reading adjustment terms as separate causal estimates. Four recommendations. "Regression tables are not a menu of modifiable risks."
• "Revisiting the Table 2 fallacy: … preeclampsia and preterm birth." (2018) — PMID 29782045 — 2,963,888 California singleton births (2007–2012). An example demonstrating with the same data that three coefficients in a single model were of different types.
• "Interpreting mutual adjustment for … socioeconomic position…" (2019) — PMID 30606167 — Under the assumption that education leads to occupation, and education and occupation together determine income, the three coefficients are of different types and cannot be directly compared. However, adjusting for the more distal indicator may be sufficient to prevent unmeasured socioeconomic confounding, which can actually increase confidence in the more proximal indicator.
• "Table 2 Fallacy in Descriptive Epidemiology…" (2023) — PMID 37444042 — A five-step framework for machine learning in descriptive research. The authors discuss strengths and weaknesses together.

Unmeasured and Residual Confounding

• "The impact of residual and unmeasured confounding…" (2007) — PMID 17615092 — Two or four normally distributed confounding variables. Under plausible assumptions, effect sizes common in observational epidemiology can be produced by confounding alone. Measurement error in confounding variables creates residual confounding of uncertain direction.
• "Residual Confounding in Health Plan Performance Assessments…" (2022) — PMID 34978862 — Medicaid natural experiment of 137,933 individuals (31.1% self-selection / 68.9% random assignment). The absolute difference in spending scores of $67 (95% CI $38–$123, 4.2% of the mean) decreased slightly to $62 after risk adjustment. Most other metrics were similar. Limitations include plan-effect heterogeneity between the two populations.