The Variables You Must Not Adjust For — Some Covariates Change the Answer the Moment You Add Them

The story begins with babies admitted to ten level III neonatal intensive care units in Lombardy, Italy, between 1999 and 2002. The babies were born between 23 and 32 weeks of gestation and weighed less than 1,500 grams. Of the 1,314 infants, 1,118 survived to 36 weeks of postmenstrual age, and 15.9% of them developed a lung disease called bronchopulmonary dysplasia. 82% of the babies received steroids through their mothers before birth.

The researchers asked whether those steroids prevented this lung disease. When the two groups were simply compared, there was no difference unlikely to be due to chance — in other words, no significant protective effect. However, when they ran two statistical models that calculated the effect by including multiple variables all at once, the answers split. The variables that split the answer were mechanical ventilation, severity score, and patent ductus arteriosus.

When these three were left out of the model, the risk for babies who received steroids was lower. The odds ratio was 0.59. The odds ratio is a metric covered in "An Odds Ratio Is Not a Risk Ratio — What the 'Times More Likely' Is a Multiple Of", which divides the odds of an event in two groups; a value less than 0.59 means the risk is lower in the exposed group. The 95% confidence interval, which is the range likely to contain the true value, was 0.36–0.97, and P = 0.036. Conversely, when the three were included in the model, the effect of the steroid disappeared (PMID 17564592).

It is the same data, the same exposure, and the same outcome. Here, the exposure is what is suspected as the cause (steroids), and the outcome is the event we want to know about (lung disease). Whether three variables were included or excluded split the answer.

Adjustment is the act of putting a variable into a model and calculating the results as if comparing people with the same value for that variable. The common paper line "adjusted for age, sex, and BMI" reads like a report that the influences of those variables have been erased. In reality, it is a claim about where those variables are positioned between the cause and the outcome. This idea is elaborated in "What "Adjusted for Age, Sex and BMI" Actually Did — How to Read Confounding and Adjustment".

Whether or not to adjust is decided by where the variable stands. There are three positions.

• Confounders are variables that cause both the exposure and the outcome. "If People Who Take It Live Longer, How Were They Different to Begin From? — Confounding" covered this position.
• Mediators are variables on the pathway through which the exposure causes the outcome. The exposure changes the mediator, and the changed mediator changes the outcome.
• Colliders are variables influenced by both the exposure and the outcome. The name comes from how two arrows collide at this variable.

This article follows mediators and colliders. Adjusting for a mediator makes an existing effect disappear or reverses its direction. Adjusting for a collider creates an association that was not there.

This article does not advise making fewer adjustments. Below, we will also see cases where bias was cleared away by making more adjustments.

⚠️ The medications, diseases, and figures appearing below are all examples to demonstrate how to read numbers. They are not judgments on which treatments are good or bad, and each number has meaning only within the design, subjects, and time frame of that study.

How Common Is Misplaced Adjustment?

Adjusting for variables that should not have been included is called overadjustment. Overadjustment is common. Out of 175 cohort studies on long-term air pollution and health, 122 of them (69.7%) showed the possibility of overadjustment. A cohort study is a study that follows a group of people over time. The subjects were papers published in high-impact journals from January 2021 to October 2023, and reviewers judged the basis on which each paper selected its variables.

Among them, 120 papers (68.6%) adjusted for mediators. The remaining 2 papers (1.1%) adjusted for both mediators and colliders together. The most commonly adjusted mediator was body mass index in 98 papers (56.0%), followed by hypertension in 25 papers (14.3%).

Studies that used causal diagrams had fewer overadjustments. A causal diagram is a drawing that uses arrows to record which variable is considered to cause which variable. Only 26 studies (14.9%) used this drawing. The overadjustment rate of those 26 papers was 42.3%, which was significantly lower than the 74.5% of studies that did not use it (PMID 41671745).

Papers that gather and review multiple studies are in a similar situation. A systematic literature review is the work of comprehensively gathering and reviewing studies on a single question using a set method, and a meta-analysis is the work of combining those results numerically. There is a result from searching and reviewing 84 such papers (47 literature reviews, 37 meta-analyses) dealing with the association between socioeconomic status and health up to April 2021.

Defining exposure and outcome clearly was 73%, but all remaining items were under 55%. Defining confounders and mediators separately was 5%. Drawing a causal diagram was 2%, and reporting the adjusted variables was 35%. When evaluating the risk of bias for each study, including confounding as an item was 54%, but including overadjustment was 2%. This means that while confounding is checked, overadjustment is rarely checked.

The reason the authors view this as serious is that overadjustment bias is likely to cause the magnitude of health inequality to be estimated with bias, and designing interventions requires that magnitude to be accurate (PMID 38129958).

① Adjusting for a Variable on the Pathway — Overadjustment

Overadjustment is putting a variable into the model that should not have been put there. The name sounds like "we adjusted too much," but the problem is the position, not the count.

In the newborn case earlier, mechanical ventilation, disease severity, and patent ductus arteriosus were things that steroids reduced, and at the same time, risk factors for lung disease. In short, they were mediator variables on the pathway where steroids produced their effect. Putting these three into the model means comparing babies who have the same value on the pathway. Then what steroids did through the pathway gets left out of the calculation, and only "what is left after removing the pathway" remains. That leftover was not what the researchers asked about.

The authors' conclusion is the same. Adjusting for a variable that can be a mediator on the causal chain can obscure the ability to detect the protective effect of a treatment. And in these data, the effect of steroids appears to be mediated in part through reducing classical risk factors (PMID 17564592).

The term overadjustment was used inconsistently for a long time, and a 2009 paper cleared up its definition. Overadjustment bias is controlling for an intermediate variable on the causal path from exposure to outcome, or a proxy variable branching off from that intermediate variable. An intermediate variable is a variable in the same position as a mediator, and a proxy variable is one that is influenced by the intermediate variable and displays its value in its place.

The same paper distinguishes between overadjustment and unnecessary adjustment. Unnecessary adjustment is controlling for a variable that does not affect bias, but can affect precision. The authors showed this distinction using the effect of maternal smoking on neonatal mortality as an example, and measured the magnitude of bias through simulation. The bias of overadjustment comes from a causal structure different from confounding or selection bias, and is not a problem caused by a small sample. Inefficiency caused by unnecessary variables, by contrast, varies depending on sample size (PMID 19525685). This means that even if you increase the sample, the bias of overadjustment does not disappear.

An Example Where the Direction Flipped

Overadjustment does not stop at making an effect look faint. There are also cases where the sign of the effect flipped.

Babies born small for their gestational age are called small for gestational age infants. Studies asking whether being born small for gestational age causes later obesity have concluded that it is associated with increased fat mass in childhood and adulthood. However, those analyses "adjusted" for height, weight, and body mass index measured at the same time when measuring obesity. These measurements are mediators that may lie on the pathway from being born small to fat mass.

To see the bias from this practice, a study ran two analyses side by side using the same data. The data come from the Belarusian infant cohort born in 1996–1997 and followed up to age 11.5 in 2008–2010. Fat mass was body fat measured by skinfold thickness and bioelectrical impedance.

The first analysis adjusted only for variables measured at baseline. Here, being born small for gestational age showed a negative (-) association with all fat mass outcomes. This means the fat mass of children born small tended to be lower instead. The second analysis additionally adjusted for concurrently measured weight or body mass index. Then the association flipped to positive (+). This matches the direction of previous studies that concluded fat mass was higher.

The authors also treated these measurements as mediators and estimated the controlled direct effect. The controlled direct effect is the effect of the exposure that remains when a mediator is fixed at a certain value. When modeled by height, this effect was similar to the first analysis. When modeled by body mass index, it was a null value, meaning no effect. When modeled by weight, it was confounded by the difference between fat-free mass (body weight minus fat) and fat mass within the weight (PMID 28338874).

What flipped is when weight or body mass index measured at the same time the fat mass was measured was included in this single cohort. This is not a general rule that "adjusting changes the sign." However, the same variable appears so often that it is hard to dismiss as individual authors' carelessness. Among 175 air pollution cohorts, the most commonly adjusted mediator was body mass index (PMID 41671745).

So How Do You Choose? — Covariate Selection

Covariate selection is the work of deciding which variables to put into the model. Covariates refer to variables put into the model alongside the exposure. In the earlier survey of 175 papers, only 26 papers (14.9%) used causal diagrams when choosing variables (PMID 41671745). The rest usually choose them through statistical procedures. This looks like putting in significant variables, or putting in variables whose estimates move a lot when they are added.

Yet even variables in the wrong place move the estimate a lot when put in. The newborn case where adding three mediators made the effect of steroids disappear is an example of that. The fact that an estimate moves is no reason to include that variable.

Three steps are suggested as the order for choosing variables. First, make the research question and the causal effect of interest clear. Second, use expert knowledge and theory to draw a causal diagram of the assumptions about the relationships among the variables. Third, based on that diagram, choose a set of variables that maximizes adjustment for confounding and minimizes adjustment for mediators. The social epidemiology (the field dealing with social conditions and health) introductory paper that proposed these three steps notes that overadjustment bias remains a common yet underrecognized problem in social epidemiology (PMID 35662623).

There are more formal rules as well. The modified disjunctive cause criterion introduced by an epidemiology methodology tutorial chooses variables through three rules. Among variables preceding the exposure, all those that affect the exposure, the outcome, or both are included. Variables that affect only the exposure and reach the outcome only through the exposure are excluded. If the common cause of the exposure and the outcome could not be measured directly, a proxy variable for it is included.

A warning from the same tutorial also belongs to this section. Even if the sample is large and the estimates gather in a narrow range, if there is systematic error, that estimate can be precisely inaccurate (PMID 38972732). This means the narrow range may be gathered in the wrong spot.

② When We Adjust for a Variable Affected by Both Exposure and Outcome — A Phantom Association Appears

Adjusting for a mediator made the existing effect disappear. Conditioning on a collider does the exact opposite, creating a phantom association. Conditioning on a variable means selecting only people who have a specific value for that variable, or putting that variable into a model to compare people with the same value. A collider is a variable that both the exposure and the outcome affect.

Collider bias is the skew that occurs when we condition on a third variable that is affected by both of the other two (PMID 29040562). When we select people based on that variable, an association that did not exist between the two variables arises within that selected group, or the existing association gets distorted (PMID 33184277).

Why this happens is easy to see with a common example. Let us say that people are admitted to a certain hospital if they have at least one of two diseases. If we gather only hospitalized people and look at them, someone who does not have one disease is very likely to have been admitted because of the other. Therefore, two diseases that had no relationship with each other outside appear inversely related among hospitalized patients, such that having one makes having the other less likely. This is because we selected people using hospitalization as a collider.

An Example Where the Conclusion Flipped

The conclusion can flip just based on how the control group is chosen. To show this, a 2026 study examined rotator cuff tears using anonymized electronic health records (computerized medical records from hospitals). This is a method where a patient group with the disease and a control group without it are gathered, and it is compared in which group the suspected exposure was more common.

Rotator cuff tears commonly require imaging tests for diagnosis. Therefore, there has been an argument that the control group should also be selected from people who received imaging tests to be fair. However, having received an imaging test means there were symptoms, and symptoms are a variable pushed up together by both the exposure and the outcome—in other words, a collider. Whether or not an imaging test was performed is a variable extending from that collider.

The research team separately assembled a control group chosen only from people who received imaging tests and a control group without that condition, and measured the associations of body mass index, type 1 diabetes, and type 2 diabetes with rotator cuff tears side by side.

The patient group was older than the control group, and had more arthritis (57%), ligament disease (9%), and previous shoulder injury (99%). The control group that required imaging tests more closely resembled the patient group. When comparing the imaging control group and the non-imaging control group, arthritis was 9% versus 1%. Ligament disease was 6% versus 2%, and previous shoulder injury was 54% versus 7%. The prevalence of type 1 diabetes was 3% in the patient group, 4% in the imaging control group, and 1% in the non-imaging control group (national level approximately 1%).

Among the three exposures, the answer split for type 1 diabetes, whose results the abstract reported. Using the control group that did not require imaging tests showed a positive association (adjusted odds ratio 1.78, 95% confidence interval 1.64–1.92). An adjusted odds ratio is the odds ratio after adjusting for other variables. Using the control group that required imaging tests showed a negative association (0.75, 0.57–0.97) (PMID 42223248). The same data, the same exposure, and the same outcome, yet the conclusion reversed solely due to how the control group was defined. That is precisely what the authors intended to show with this study. Simply conditioning on a variable extending from a collider can sway the estimate enough to flip the conclusion.

Who Got Into the Sample Is Already Adjustment — Selection Bias

Selection bias is skew created by who got into the sample. Selection bias happens even without putting variables into the model. Imposing an imaging test condition on the control group in a rotator cuff study is an example. The moment that condition is imposed, the analysis takes place only among "people who received an imaging test," and a relationship that was not originally there appears within that group.

There is also a proposal to unify the definition of selection bias into one. The idea is to call the population before selecting the sample the reference population, and to call any skew that deviates from the true causal effect of the reference population because the sample was selected from there selection bias. Under this definition, there are two branches. The first branch arises from narrowing the sample by picking only one value of a collider or its descendant variable. A descendant variable is a variable affected by a collider, and whether an imaging test was done in the rotator cuff case is an example. The second branch arises from narrowing by picking only one value of a variable whose effect size varies depending on that value. The two branches can also happen together (PMID 35700187).

Just because there is selection does not mean there is necessarily selection bias. To know when bias happens, you must understand bias from conditioning on a collider. One paper points out that this bias is common, hard to recognize, and usually self-inflicted by researchers (PMID 39891549).

Studies that reuse electronic health records are especially exposed to this bias. To remain in hospital records, one had to come to the hospital. Therefore, reusing this data implicitly conditions on the common collider of medical utilization itself. This danger stems from the nature of medical access and utilization in the United States (PMID 36752649).

Large Sample Size and Representativeness Don't Make It Immune

In large cross-sectional and cohort studies, it is often assumed that even if who enters the study is skewed, only representativeness and prevalence estimation will be shaken, while association estimation will not be shaken much.

There is a paper that directly refutes this assumption. Because selection does something akin to conditioning on a collider, they showed via simulation that even a moderate degree of influence on study entry or dropout can yield skewed and misleading estimates. This was true for both phenotypic (traits that can be measured on the outside) and genotypic associations. The prescriptions are two: knowing which population the sample represents, and that if the factors influencing selection and dropout can be known, they can be adjusted for (PMID 29040562).

The same warning emerged in early COVID-19 observational studies. In UK Biobank data, participants who received COVID tests were heavily selected across multiple axes of genetic, behavioral, cardiovascular, demographic, and anthropometric traits compared to the broader cohort. The authors wrote that existing studies should explore collider bias, while concluding that the optimal mitigation is to use appropriate sampling strategies at the design stage (PMID 33184277).

The same mechanism occurs even in representative cohorts. This is because selection processes that happen in any population—such as survival, immigration, and migration—exist. Here is the conclusion of the authors who demonstrated this with data from the Piedmont region of Italy. The degree to which exchangeability breaks down varies depending on the source populations. Exchangeability is the property where two groups are similar enough that they could be swapped with each other. However, neither side is inherently less skewed. The key is whether related risk factors can be identified and controlled (PMID 30804046).

An Example of How an Apparent Protective Effect Is Created

Glucosamine is a supplement widely used for joint pain and osteoarthritis. While randomized trials, which divide groups by a draw, have been inconclusive, observational studies, which watch people as they take it, have reported significantly reduced mortality and cancer incidence. There is an analysis examining whether this benefit is explained by bias, particularly selection bias.

The analysts found 11 observational studies. Averaging the all-cause mortality reductions reported by each of those 11 studies yielded 16%. The hazard ratio is 0.84 (0.81–0.87). A hazard ratio is a value dividing the event occurrence rate at each time point between two groups. Reductions were also reported for cancer incidence, cardiovascular disease, respiratory disease, and diabetes.

The authors showed that these significant effects could stem from selection bias caused by collider stratification. Collider stratification is when people are divided or selected and analyzed based on the value of a collider. This is because all the studies formed their cohorts with people who were already taking glucosamine even before entering the cohort, and the participants were people who agreed to join the cohort.

The authors demonstrated this bias using a 500,000-person UK Biobank paper as an example. When the true incidence rate ratio in the entire population is 1.0, it could be biased to 0.82 in such a cohort. An incidence rate ratio is a value dividing the event incidence rates of two groups. This means that even though there is actually no difference, the supplement can look like it reduces mortality. The sentence in the conclusion is more definitive. These observational studies reporting significant decreases were affected by selection bias originating from collider stratification.

This study does not say that the supplement reduces or increases mortality. What the authors wrote is this. Until an observational study bypassing this bias is properly conducted targeting "people who just started taking it," studies to date cannot support prescribing this supplement for the purpose of preventing mortality, cancer, and other chronic diseases (PMID 36029480).

An Example from Genetic Epidemiology

From a large-scale dataset on the most dangerous type of malaria, this report emerged. In people with a genetic trait called G6PD deficiency, malaria affecting the brain occurs less often and severe anemia occurs more often. An explanation was attached to this. Since there are two paths of dying from malaria where the risk of one side decreases and the other increases, the explanation was that this trait is evolutionarily advantageous.

When this claim was re-analyzed using a causal diagram, it was revealed to be a target of collider bias. In a sensitivity analysis examining whether the conclusion wobbles by changing assumed values, when simulating while varying the strength of the known effect of G6PD deficiency on anemia, this bias alone was sufficient to explain all of the observed association. This means the "protective effect" against cerebral malaria could have arisen from bias alone. The authors recommend that genetic epidemiology research in this field utilize causal inference in the future (PMID 30688212).

There Is More Than One Direction — An Example Where Further Adjustment Stripped It Away

A study looking only at hospitalized COVID-19 patients already has a condition placed on a collider. This is because we only look at people who passed through the door of hospitalization. In this situation, there is a study that drew a causal diagram and compared the relationship between vaccination and COVID-19 death across three models.

In Model 1, which only included vaccination, no evidence appeared that the vaccine prevents death. In Model 2, which included age as a covariate to strip away the bias that arose because conditioning happened on hospitalization, the protective role of the vaccine was revealed. In Model 3, which additionally included chronic diseases, the protective effect became slightly stronger. The authors' conclusion is twofold. Studying hospitalized patients makes one subject to collider stratification bias. And just like confounding, this type of selection bias can also be adjusted for by including variables in the regression model that affect hospitalization and are also risk factors for the outcome (PMID 38111522).

After selection has already occurred, adjusting for the variables that influenced that selection can sometimes be the way to strip away the bias. The prescription attached by the earlier large-scale cohort paper pointed in the same direction as well (PMID 29040562). The point is not the count, but the position.

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⚠️ Collider Bias Is Not a Universal Explanation

The collider is the most entertaining concept in this article, so once you hold it in your hand, you want to apply it to every paradox. But "That paradox? It's a collider" is not what this article wants to leave you with. Three papers directly put the brakes on such a usage.

First is the obesity paradox. The obesity paradox is the phenomenon where obesity is associated with reduced mortality, contrary to expectation. A common explanation for this phenomenon is collider stratification bias. There is a study that tested this explanation using simulated data built to approximate reality. In various scenarios where exposure was obesity, outcome was mortality, and mediator was diabetes, with unmeasured confounders included, the bias was calculated using counterfactual causal analysis (a calculation comparing what would have happened had there been no exposure).

It was confirmed that collider stratification makes the estimation of causal effects biased. However, that bias was small compared to the causal relationships among the variables. The authors' conclusion is as follows. Collider bias can be a partial explanation for the obesity paradox. However, it is unlikely to be the main explanation that created an association in the opposite direction of the true causal relationship, and other explanations must be sought (PMID 27075676).

Second is the "reverse obesity paradox" in prostate cancer. This is the phenomenon where a higher body mass index is associated with fewer prostate cancer diagnoses, but more deaths caused by prostate cancer. By hazard ratio, it is a negative association with diagnosis (about 0.9 per 5 kg/m² increase) and a positive association with prostate cancer-specific mortality (about 1.2). While simulating binary (yes-no) diagnosis and mortality data, the research team included unmeasured background variables that could cause collider bias, and calculated the bias percentage as the difference between values adjusted for that variable and unadjusted ones.

Even when wide-ranging plausible values for prostate cancer were plugged in, collider bias did not distort the odds ratio between body mass index and prostate cancer mortality by more than 4%. In terms of continuous body mass index, this amounts to the odds ratio fluctuating by ±0.04. The room for distortion by classical confounding was larger than that. The authors' conclusion is as follows. Collider bias alone makes it difficult to explain the reverse obesity paradox of (especially localized) prostate cancer. This result reinforces mechanistic evidence supporting the possibility that the observed positive relationship is real, and therefore exploring other mechanisms is important (PMID 40231651).

Third is a systematic review that scanned the entire literature. Selection bias and collider restriction bias (bias arising from narrowing the sample to a single value of a collider) have been conceptually lumped together as threats to internal validity (did the study correctly estimate causal relations within its own sample?), and the starting point was that the conclusions about their impact should therefore also match. English methodology papers and general epidemiology textbooks from January 2000 to July 2024 were searched to select literature discussing the magnitude or direction of the two biases. Out of 5,508 papers and 205 textbooks, 33 papers and 12 textbooks remained.

Literature dealing with collider bias conveyed its impact as negligible, whereas literature dealing with selection bias described diverse impacts. The authors add a qualification. Most collider literature evaluated bias under the condition of assuming no relationship between exposure and outcome. Also, discussions on the role of interaction and affected strata differed between the two bodies of literature. Therefore, the authors suggest investigating collider bias under conditions without that assumption, and considering multiplicative and additive interactions among the causes of the collider together (PMID 40167168).

We add our own point here. "It was small" is not the correct answer either. In the malaria case earlier, collider bias alone was sufficient to explain the entirety of the observed association (PMID 30688212). In the rotator cuff case, the sign of the conclusion was flipped (PMID 42223248). The magnitude varies from case to case. Therefore, "This is a collider" is not the end of the explanation, but the name of the thing that must be measured. All three papers above also reached conclusions only after measuring the magnitude via simulation or literature review.

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Still Being Settled — Starting with the Name

The terminology in this field is still being sorted out. One commentary suggests dividing collider stratification bias into two. One is collider restriction bias, which arises by selecting only one level of a collider or its descendant variable to restrict the sample. The other is collider conditioning bias, which arises by including a collider in a regression model.

The gist of the commentary is this. Classifying collider conditioning bias as selection bias creates semantic confusion. This is because putting a variable into a regression model is not the same thing as choosing the sample to analyze. Therefore, the authors suggest viewing collider conditioning bias as a type of overadjustment bias (PMID 37939152).

If this suggestion is correct, the two sections of this article merge into one. Putting a mediator on the path into the model, and putting a collider affected by both exposure and outcome into the model, are both cases of putting a variable into a spot where it should not have been put.

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For Deeper Exploration

We have summarized the 21 papers cited in the "Reference Papers" below, one line per theme: 7 on overadjustment and covariate selection, 8 on colliders and selection bias, 3 putting the brakes on over-applying collider explanations, and 3 on terminology.

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When you encounter the phrase "we adjusted for," rather than asking how many variables were put in, you should ask what position those variables occupy. The list of variables printed in a table is not the only adjustment. Who was put into the sample and where the control group was drawn from do the exact same job.

If you use this rule to write a conclusion that says, "Therefore, that paradox is a collider," this article has failed. When you encounter the phrase "This is a collider," all you need to do is find the paragraph in that paper where the magnitude of the bias was measured. The answers from studies that measured the magnitude were split. In the malaria case, the bias alone was enough to explain the entire observed association, while in the prostate cancer case, it failed to distort the odds ratio by more than 4%.

Source Papers

Overadjustment

• "Overadjustment bias and unnecessary adjustment in epidemiologic studies." (2009) — PMID 19525685 — Distinction between overadjustment bias (controlling for intermediate variables on the path and their descendant proxy variables) and unnecessary adjustment (affecting only precision). It is a causal structure distinct from confounding and selection bias, and not a finite-sample bias.
• "Does Fetal Growth Restriction Cause Later Obesity? …" (2017) — PMID 28338874 — Belarus cohort (born 1996–1997 → age 11.5). Adjusting only for baseline variables yields a negative association, which reverses to positive when simultaneously measured weight and BMI are added.
• "Antenatal steroids and risk of bronchopulmonary dysplasia…" (2007) — PMID 17564592 — 10 neonatal intensive care units in Lombardy, 1,118 survivors out of 1,314 infants, BPD 15.9%. Excluding intermediate risk factors yields an OR of 0.59 (0.36–0.97), while including them causes the effect to disappear.
• "Potential over-adjustment bias in cohort studies of air pollution and health…" (2026) — PMID 41671745 — 175 high-impact journals. DAGs used in 26 papers (14.9%), potential overadjustment in 122 papers (69.7%), mediator adjustment in 120 papers (68.6%), most frequent mediator BMI in 98 papers (56.0%). 42.3% versus 74.5% when DAGs were used.
• "Overadjustment bias in SRs and MAs of socio-economic inequalities…" (2024) — PMID 38129958 — 47 SRs and 37 MAs. Exposure and outcome definition 73%, all other items below 55%. Confounder and mediator distinction 5%, causal diagrams 2%, adjustment variable reporting 35%, RoB including overadjustment 2% (confounding 54%), MA sensitivity analysis 16%.

Covariate Selection

• "Avoiding overadjustment bias in social epidemiology…: a primer." (2022) — PMID 35662623 — Three steps (clarifying question and causal effect → causal diagram → maximize confounding adjustment and minimize mediating adjustment). It also covers life-course timing and indicator mutual adjustment.
• "Methodological Tutorial Series…: Confounder Selection…" (2025) — PMID 38972732 — Modified disjunctive cause criterion. The pitfalls of adjusting for intermediate variables and baseline outcome variables. Even large samples can be "precisely inaccurate" if there is systematic error. It also introduces the E-value and robustness value (which this article does not cover).

Colliders and Selection Bias

• "Leveraging Electronic Health Record Data to Evidence Collider Stratification Bias…" (2026) — PMID 42223248 — Rotator cuff tear. Depending on the control group definition (whether imaging was required), the adjusted odds ratio for type 1 diabetes was 1.78 (1.64–1.92) versus 0.75 (0.57–0.97). Mechanism demonstrated as the authors wrote.
• "Collider scope…" (2018) — PMID 29040562 — Merely moderate selection and dropout can bias phenotype-genotype association estimates.
• "Healthcare utilization is a collider…" (2023) — PMID 36752649 — Reusing EHRs implicitly conditions on healthcare utilization, a collider. DAG recommended at the design stage.
• "Collider bias undermines our understanding of COVID-19…" (2020) — PMID 33184277 — UK Biobank test takers were heavily selected across multiple trait axes. Optimal mitigation is design-stage sampling.
• "Baseline selection on a collider…" (2019) — PMID 30804046 — Due to selection processes like survival and migration, the same mechanism happens even in a "representative cohort" (Piedmont data). Neither side is inherently less biased.
• "Glucosamine…: Selection bias in the observational studies." (2022) — PMID 36029480 — An average 16% reduction in all-cause mortality reported across 11 observational studies (hazard ratio 0.84, 0.81–0.87). Reductions also reported for cancer, cardiovascular disease, etc. UK Biobank demonstration shifted the true incidence rate ratio from 1.0 to 0.82.
• "Collider bias and the apparent protective effect of G6PD deficiency on cerebral malaria." (2019) — PMID 30688212 — Re-analyzing a new form of the balancing selection hypothesis. Bias alone is sufficient to explain all of the observed association.
• "Adjustment for collider bias in the hospitalized Covid-19 setting." (2023) — PMID 38111522 — Exposure is vaccination. Model 1 (vaccination only) → 2 (age) → 3 (chronic conditions) revealed and slightly strengthened the protective role. Like confounding, this selection bias can be adjusted for by including variables.

Applying the Brakes to Overapplication

• "Collider Bias Is Only a Partial Explanation for the Obesity Paradox." (2016) — PMID 27075676 — Collider stratification creates bias, but it was small compared to the causal relationships between variables. It is a partial explanation, but unlikely to be the primary explanation that reverses the direction.
• "Collider Bias Is an Insufficient Explanation for the Inverse Obesity Paradox in Prostate Cancer." (2025) — PMID 40231651 — BMI is negative with diagnosis (HR about 0.9/5 kg/m²), and positive with specific mortality (about 1.2). It failed to distort the odds ratio by more than 4% (±0.04). The conclusion was that the room for classical confounding was larger, reinforcing the possibility that the positive relationship is real.
• "The Same but Different?…" (2025) — PMID 40167168 — 33 out of 5,508 papers and 12 out of 205 textbooks. Collider literature conveys minimal impact, while selection bias literature is described in various ways. Most evaluated under the assumption of an exposure-outcome independence.

Terms Are Being Sorted Out

• "Selection Bias Requires Selection…" (2024) — PMID 37939152 — Distinguishes between collider restriction bias and collider adjustment bias, proposing to view the latter as a type of overadjustment bias.
• "Toward a Clearer Definition of Selection Bias…" (2022) — PMID 35700187 — Unifies the definition as a distortion deviating from the true causal effect in the reference population. Type 1 (collider restriction) and Type 2 (restriction on effect modifiers).
• "When selection becomes selection bias." (2025) — PMID 39891549 — Selection is not necessarily selection bias. Collider-conditioning bias is common and usually self-inflicted.