What Is Left After Adjustment — What E-values, Negative Controls and Propensity Scores Do and Do Not Do

There is observational data on prenatal care and low birth weight. Observational data is a record of what care people already received and what happened afterward, without a lottery. In this data, an association appeared between the degree of prenatal care and low birth weight. The researchers added one more calculation to this: "For this association to be due to something else we didn't measure rather than cause, how strong would that factor have to be?"

The answer was between 1.45 and 5.63 depending on which category of which index you looked at. The authors read this value as follows: an unmeasured factor would have to be strong enough to raise the risk of low birth weight by over 400% to fully explain the observed association (PMID 34190835).

A number that answers this question of "how strong an unmeasured factor needs to be to erase the result" is called an E-value.

This question comes from confounding and adjustment. Confounding is when an external factor that affects both the treatment and the outcome creates a fake association between the two. Adjustment is the act of matching the original differences between two groups through calculation and then comparing them. A single line reading "adjusted for age, sex and BMI" is a claim that those variables were placed in a specific slot between the cause and the outcome, and picking the wrong slot makes adjustment create bias instead. How to choose those slots is handled by "What "Adjusted for Age, Sex and BMI" Actually Did — How to Read Confounding and Adjustment" and "The Variables You Must Not Adjust For — Some Covariates Change the Answer the Moment You Add Them".

However, there is a problem that remains even if you pick all the slots correctly. Variables you did not measure cannot be adjusted for, and variables you measured incorrectly are only adjusted for halfway. Confounding that remains even after doing all such adjustments is called residual confounding. This name also appeared in "If People Who Take It Live Longer, How Were They Different to Begin With? — Confounding". Residual confounding is why almost every observational study paper closes its final paragraph with "unmeasured confounding cannot be ruled out."

This article deals with what comes after that sentence. Researchers have built tools to measure the size of the remaining confounding, and within the same literature, they are also measuring the limits of those tools. There are four new terms to learn, and each term is defined where it first appears.

⚠️ The names of drugs, vaccines, and procedures appearing below are all examples just to show how to read numbers. They are not judgments on whether a specific treatment is good or bad, and each number has meaning only within the subjects and data source of that study.

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E-value — How Strong a Confounder Would It Take to Erase This Result?

The E-value is the minimum strength of association that an unmeasured confounder would need to have with both the treatment and the outcome to fully explain away an observed treatment-outcome association. It is measured on the risk ratio scale, which is the value obtained by dividing the proportion of people who experienced the event between the two groups, while leaving variables you have already adjusted for as they are. The value from the prenatal care example at the beginning is also measured on this scale.

If the value is large, a strong confounder is needed to erase the result, and if it is small, even a weak confounder can erase it (PMID 28693043).

The authors who proposed this metric recommend that all observational studies aiming for causal evidence report the E-value or use other sensitivity analyses. A sensitivity analysis is an additional analysis to check whether the results hold up even if the assumptions are changed. The authors add that the E-value should be calculated twice: once for the observed estimate, and once for the end of the confidence interval closer to the null value (PMID 28693043). A confidence interval is the range in which the estimate can fluctuate due to chance, and the null value is the value meaning "no effect".

An example that pushes this logic to its limit is the COVID-19 vaccine. It examined whether the vaccine effectiveness estimates from observational studies could be explained by unmeasured confounding alone (PMID 41343587). Looking at when the observed risk ratio was 0.08, meaning the disease was much rarer in the vaccinated group, the confounding variable to explain it had to meet two conditions together. It had to be heavily imbalanced between the vaccinated and unvaccinated groups, and at the same time be a factor that strongly prevented the disease. The example the authors gave is being 10 times more common in the vaccinated group and lowering the disease risk by 99%.

In a simulation where the strength of the confounding variable was randomly drawn across a wide range, the cases satisfying that condition were less than 2%, and even for the more moderate risk ratio of 0.25, they were less than 6%. The authors' conclusion is that while residual confounding can weaken the effect estimate, it is statistically and epidemiologically implausible for unmeasured confounding alone to explain the entire observed effect size (PMID 41343587).

What to look at in this example is how the tool is used. The counterargument "there might be something we didn't measure" turns into the answerable question, "How strong would that unmeasured thing have to be?"

The same literature also notes the limitations of this tool. The E-value has three advantages: it requires no additional assumptions, it is easy to calculate, and reporting it routinely increases transparency. It also has three limitations. There is no universal cutoff for interpretation, meaning no common standard that says "you are safe if you exceed this value." Other biases besides confounding cannot be factored into the calculation. There is room to selectively report only favorable values (PMID 42264181). Therefore, the authors recommend reporting the E-value within the context of the study and the confounding variables already adjusted for, and having researchers explicitly point out plausible unmeasured confounding variables (PMID 42264181).

Why this demand to point them out is attached is shown by actual usage practices (PMID 31930286). Up to the end of 2018, 87 papers that presented E-values in their data produced 516 values. Only 19 of them compared that magnitude to the strength of confounding expected in their field.

Looking by the authors' own judgments, the median for the 43 values where the authors judged that "confounding likely affected the result" was 1.88. For the 348 values where they judged it "unlikely to have affected the result," it was 1.82, and for the 125 with no mention, it was 2.02. The magnitudes of the E-values practically overlapped regardless of the authors' judgments.

The authors' conclusions are three. As calculation becomes easier, already shoddy handling of confounding could get worse. The E-value cannot replace carefully examining the sources of unmeasured confounding. If you use it, you must interpret it within the context of confounding expected in each field (PMID 31930286).

Negative Control — When an Impossible Association Appears, It Is a Signal

A negative control is a verification step where researchers intentionally choose an exposure or outcome that cannot possibly be the cause, and check whether an association still appears. If an association appears there, it is a signal that confounding, recall bias, or an analysis error exists somewhere. Recall bias is a distortion that occurs when people remember and answer about the past.

This device came from the laboratory. To see if a reagent is working properly, laboratories run a condition alongside where a reaction should not possibly occur. If a reaction appears there, they suspect the equipment rather than the reagent.

The authors who brought this concept into epidemiology distinguished between two types. One is an exposure-side control placed in the cause position, and the other is an outcome-side control placed in the result position. After giving examples for each, the authors conclude that negative controls should be used more commonly in observational studies. However, they add the caveat that more research is needed on under which conditions it sensitively catches other sources of error (PMID 20335814).

A negative control does two things. Detection is noticing that bias exists, and correction is adjusting the estimate by that much bias. Detection tells us little, and correction demands much. If there is an association between the negative control and the variable of interest, we can know up to the point that something—confounding, selection bias, or information bias—is present. However, correction requires much stricter mathematical assumptions such as rank preservation, monotonicity, and linearity (PMID 38040387). Counting 37 methodological papers by function, there were 14 for bias detection, 16 for bias correction, and 5 for p-value and confidence interval adjustment (PMID 38040387).

Actual usage also follows this line. Among 184 pharmacoepidemiology papers, 149 (81%) used negative controls for bias detection, and 16 (9%) used them for bias correction. The authors conclude that while negative controls are a powerful tool for bias detection, many studies failed to verify the assumptions underlying them (PMID 37851862).

Detection also has limitations. Negative controls can lack both specificity and sensitivity for catching unmeasured confounding. Here, sensitivity is the ability to catch confounding that actually exists, and specificity is the ability not to claim confounding exists when it does not. Also, proving that "there is no association in the negative control" is impossible to begin with (PMID 37338976). The authors of this overview walked through the assumptions of three correction approaches and the impact when those assumptions are broken. And while they view that future research can broaden the scope of application, they conclude that for now, careful judgment must be made on a case-by-case basis (PMID 37338976).

How Often Are the Tools Actually Used?

More than nine out of ten papers mentioned worrying about residual confounding, but only about half actually measured it. The reviewed set consisted of 158 active comparator cohort studies published in 12 medical and epidemiological journals between January 2017 and June 2022 (PMID 39098826). Active comparator studies are studies that compare a drug of interest not to "people who didn't take it," but to people who took a different drug used for the same indication. An indication is the patient's condition that serves as the reason to use that treatment.

Among these, residual, unmeasured, or uncontrolled confounding was mentioned as a potential concern in 93%. However, sensitivity analyses evaluating confounding due to unmeasured variables were actually performed in at least some capacity by 84 papers (53%). The most common method was the E-value in medical journals (21%), and restriction—narrowing down subjects using measured variables—in epidemiological journals (22%) (PMID 39098826).

The methods are already organized. There is an overview dividing methods for handling unmeasured confounding into the design phase, analysis phase, and substudies that collect more confounding variable information from a subset of subjects, and its authors conclude that statistical evidence and clinical knowledge should be used together for interpretation (PMID 27091131).

And When You Actually Measure It, Residual Confounding Is Sometimes Small

The tools above do not end with "we can never know." We can measure the size of remaining confounding with actual data, and when we measured it, it turned out to be "small."

That data links insurance claims data with electronic health records. Because claims data are records left behind to bill for medical care, information that exists only in health records—such as lab values—is not captured well. There is a proof-of-principle study—a pilot study showing whether the method works—that used this linked data at the Mass General Brigham site of the U.S. FDA Sentinel Real-World Evidence Program.

The proxy variables created from claims data—variables that stand in for things that were not measured directly—were already balancing out most of the risk factors that could be measured only through health records. Therefore, in this example, it was judged unnecessary to correct for residual confounding using quantitative bias analysis (PMID 41708481). Quantitative bias analysis is a method that corrects an estimate by guessing the size and direction of bias using external information.

Another study created 500 simulated cohorts using the same linked data from the same site. The researchers intentionally created residual confounding by using confounding variables that were missing from claims data but present only in health records. In both sets of results, when adjusting for claims-data-based variables, the relative bias was close to 0. Relative bias measures the ratio of how far the adjusted estimate deviates from the true value. The authors' conclusion was that within realistic simulations based on empirical data, confounding variables absent from claims data were unlikely to create strong residual confounding (PMID 42093129).

Both studies came from the same linked data at the same FDA Sentinel Mass General Brigham site, and each is a result within a specific drug comparison. They are not two independent replications, nor do they mean that the same answer comes out with different questions and different data. The authors add that for routine checks like this, a data infrastructure linking claims data and health records must be in place (PMID 41708481). There is one takeaway from the two studies. The saying "unmeasured confounding cannot be measured" is not true.

Why Did That Person Get That Treatment? — Confounding by Indication

Confounding by indication is confounding that happens because the reason someone received a treatment—in other words, the patient's condition—also affects the outcome. In observational studies, who gets a treatment is decided by doctors, not by a coin toss. And sick people receive drugs. So if the results are bad in the group that got the drug, the data alone cannot separate whether it was because of the drug or because of the illness.

The stubbornness of this bias is shown by data from elderly breast cancer patients (PMID 19457638). In the medical records of 1,798 patients diagnosed between 1990 and 1994, the recurrence rates were compared between the group that received adjuvant chemotherapy and the group that did not. In the unadjusted analysis, chemotherapy had a positive association with recurrence. The hazard ratio was 2.6 (95% CI 1.9–3.5). The hazard ratio is the value obtained by dividing the rate at which events occur between two groups.

The authors, who had expected a protective effect, viewed this as confounding by indication and attempted adjustments in several directions. After narrowing the subjects to a high-risk recurrence group (946 patients) and running a multivariable regression, the hazard ratio became 1.1 (0.7–1.6). Propensity score adjustment yielded 1.3 (0.8–2.0). The propensity score is a value calculated as the probability that a person received that treatment, which is covered separately in the section below. An instrumental variable-like method yielded 0.9 (0.2–4.3). An instrumental variable is a method that uses as a lever a third variable that affects the treatment but does not directly affect the outcome.

The authors' conclusion is this — conventional methods fail to control for unmeasured factors, and when dealing with confounding by indication, those factors often remain important. Propensity score and instrumental variable analyses may be useful in specific situations, but in this study, neither method adequately controlled for confounding by indication (PMID 19457638). Even in the instrumental variable method, imbalances in measured factors remained across instrumental variable levels, suggesting residual confounding. The estimate dropped from 2.6 to 1.1–1.3, but no method reliably showed the protective effect the authors had expected. These numbers do not mean that chemotherapy increases recurrence, nor do they mean it has no effect.

The same problem has been quantified in vaccine effectiveness literature. We revisit the influenza vaccine investigation seen in "If People Who Take It Live Longer, How Were They Different to Begin With? — Confounding", but this time we also look at how much the adjustment moved the numbers (PMID 26474974). Among 23 observational studies reporting influenza vaccine effectiveness, 19 (83%) showed a high risk of bias. The researchers calculated the ratio of odds ratios before and after adjustment to see what the adjustment did. The odds ratio is the value obtained by dividing the odds of an event occurring versus not occurring between two groups.

Adjustment raised the vaccine effectiveness estimates on average. That is 12% (95% CI 7–17%) for all-cause mortality, 9% (4–14%) for all-cause hospitalization, and 7% (4–10%) for influenza-like illness. Yet even after adjustment, 9 studies showed significant effect estimates outside of epidemic periods, suggesting residual confounding. During times when influenza is not circulating, there is almost no influenza for the vaccine to prevent, so the effects seen then are read as coming from differences other than the vaccine. What the researchers were trying to gauge with this comparison was healthy vaccinee bias, which is the skew that arises because people who get vaccinated are healthier to begin with.

The authors' conclusion is that while adjustment can correct for confounding by indication to some degree, the estimates remain vulnerable to healthy vaccinee bias—at least as long as non-specific outcome variables like all-cause mortality are used. A non-specific outcome variable is an outcome that counts all causes, not just influenza. And the authors go a step further — their recommendation is that administrative data-based cohort studies using non-specific outcome variables should no longer be used to measure influenza vaccine effectiveness. What to take away from this is not a judgment on vaccines, but the line the authors drew themselves on how far adjustment goes and where it stops (PMID 26474974).

There are also designs that reduce confounding by indication. Clinical indications vary by patient and are complex, making them difficult to measure accurately in non-experimental studies. However, if you restrict the study population to patients who have the indication for that treatment, the exposed group and the comparison group become comparable in terms of their probability of receiving that treatment. When indications cannot be measured precisely, a common practical solution for performing that restriction is using an active comparator, meaning another drug used for the same indication, as the comparison target, as we saw earlier (PMID 35019190). When you overlay this with the approach of enrolling people into the cohort starting from the exact moment they begin treatment, the validity of the observational study increases, bringing it closer to a randomized trial (PMID 25800216).

Observational studies have one more trap that comes from time. Depending on how exposure is defined, a follow-up period during which the outcome by definition cannot happen may be tacked onto the exposed group. This is called immortal time bias. Who is counted and starting when is covered entirely by "When Did the Clock Start for These People? — How Observational Studies Manufacture Effects".

What Propensity Scores Do and Do Not Do

A propensity score is the probability that a person will receive that treatment. When you know a person's baseline characteristics, it summarizes the extent to which they were likely to receive that drug into a single number. Propensity scores have been increasingly widely used as a method to adjust for confounding in observational studies (PMID 28104076). Methodological overviews require authors to state the assumptions and limitations of this method (PMID 37481434).

Multivariable regression, a common adjustment method, models the relationship between covariates—that is, the baseline characteristics put into the adjustment—and the outcome. The propensity score models the relationship between covariates and treatment assignment, meaning who received that treatment. Therefore, the propensity score is not constrained by the number of outcome events, making it useful when there are many confounding variables or few outcome events (PMID 29684154).

There are four ways to use it. They are matching people with similar scores, stratification by grouping and comparing score ranges, weighting (inverse probability weighting) by inverting the score to give each person a weight, and covariate adjustment by putting the score in as a single variable (PMID 29684154).

Propensity scores only deal with measured covariates. Being well-matched means being well-matched on what was measured, not that unmeasured things were matched as well. Simulations reconfirmed previous findings that propensity score matching and weighting can actually increase the imbalance of unmeasured (unmeasured) confounders (PMID 38539082).

Propensity scores were also not always better than regression adjustment. When compared using data from four large-scale cardiovascular observational studies, stratification performed poorly when outcome events were few. Inverse probability weighting produced inaccurate treatment effect estimates when there was substantial confounding. Covariate adjustment and matching worked well in all examples, but matching lost precision in some cases. The authors' conclusion is that propensity score methods are not necessarily superior to conventional covariate adjustment, and care must be taken in choosing the most appropriate method (PMID 28104076).

There are also other weighting methods proposed to be used where inverse probability weighting becomes unstable. Those spots are data with poor overlap, meaning data where the score distributions of the two groups do not overlap well. The authors write that such weighting methods can be seen as a favorable approach in those data. A final recommendation is that presenting the results of multiple propensity score methods together helps evaluate how robust the results are (PMID 40779360).

Reporting practices have also been surveyed (PMID 25433444). From December 2011 to May 2012, there were 296 papers using propensity scores published. Among them, 102 papers (34.4%) explicitly reported how variables to be put into the model were chosen. Covariate balance, meaning checking and reporting whether the characteristics of the two groups actually became similar after adjustment, was done and reported in 177 papers (59.8%). The authors' conclusion is that the performance and reporting of covariate selection and balance evaluation are far from optimal (PMID 25433444). Even practical guidelines introducing propensity score matching as a "valuable method to achieve quasi-randomization" include a checklist of reporting items. This is because any study's conclusion is only as strong as its methods (PMID 34547404).

Even Randomized Trials Adjust — But for a Different Purpose

Covariate adjustment is also used in randomized controlled trials, and major regulatory agencies recommend it (PMID 42285376). Cluster randomized trials are trials that draw lots using groups like hospitals or villages instead of individuals as the unit, and when 300 such trials were investigated, 219 of them included an adjusted analysis of the primary outcome—meaning the most important result predetermined by the trial (PMID 25648791).

The purpose of adjustment in a randomized trial is precision, specifically to reduce the margin of fluctuation in the estimate. This is because when random assignment is done well, confounding is generally not a problem. The gist of guidance issued by the U.S. FDA in May 2023 is that a pre-specified primary analysis adjusting for covariates can have advantages over an unadjusted analysis and is generally acceptable (PMID 41474130). The conclusion of the methodology overview points in the same direction but scales down the expectation. It states that adjusting for prognostic covariates yields a modest gain in statistical power, meaning the likelihood of catching a difference that actually exists (PMID 41988813).

The magnitude of the benefit was remeasured using individual-level data from 50 published randomized trials (PMID 42285376). There were 29,094 participants and 574 treatment-outcome comparisons. Comparing several adjusted estimators and three covariate selection strategies, adjustment improved precision in most situations. The variance, which represents the fluctuation of estimates, was reduced by a median of 13.3% for continuous outcomes and 4.6% for binary outcomes that split into yes/no.

The decisive result of this study is that a parsimonious regression approach using a pre-specified minority of prognostic covariates performed as well as or better than more complex methods, especially in small- to medium-scale samples. Machine learning-based estimators did not yield additional precision. The authors' conclusion is that this efficiency gain appeared consistently without introducing systematic bias, which is why they recommend routinely adjusting for covariates in primary analyses (PMID 42285376).

However, problems arise if an accidental imbalance between the two groups is noticed after the fact, and the decision of whether to adjust is made to match that direction. A study demonstrating this used data from a large statin secondary prevention trial, simulating a scenario where the drug actually had no effect (PMID 34454099). Unadjusted analyses yielded valid p-values regardless of accidental imbalances between the two groups. A p-value is the probability that a difference this large or larger would occur by chance when there is no true effect. Changing to an adjusted analysis without knowing the direction of the imbalance also did not introduce bias. But when the decision was made after looking at the direction of the imbalance, the risk of falsely declaring the experimental treatment superior became inflated. In the scenarios investigated, that risk grew by up to 48% (PMID 34454099).

The reality of practice diverges from guidelines. Out of 219 papers featuring adjusted analyses in the aforementioned review of 300 cluster randomized trials, only 71 (32%) reported pre-specifying their covariates (PMID 25648791).

Common Misconceptions

① "You Can't Trust Observational Studies"

Going from the limitations above to this conclusion is going too far. An example that asked the same question using two designs shows why.

There is a meta-analysis collecting studies comparing drug-eluting stents and bare-metal stents up to February 2008 (PMID 19528338). It analyzed 22 randomized trials (9,470 people) and 34 observational studies (182,901 people) separately. The hazard ratio for all-cause mortality was 0.97 (95% CI 0.81–1.15) in the randomized trials, with no detectable difference. In the observational studies, it was a significant decrease at 0.78 (0.71–0.86). Myocardial infarction also split in the same direction (0.95 versus 0.87).

Target vessel revascularization is a procedure to reopen a blood vessel that has narrowed again after the initial procedure. For this outcome, the randomized trials showed a significant 55% reduction at 0.45 (0.37–0.54), and the observational studies showed a reduction of 0.54 (0.48–0.61).

Let us first translate the authors' conclusion — that both randomized trial and observational designs showed a clear and similarly sized reduction in target vessel revascularization with drug-eluting stents compared to bare-metal stents, and that this entire body of data suggests drug-eluting stents are safe and effective both within and outside approved indications while highlighting the differences between randomized and observational data. The authors also explicitly note the possibility of selection bias and residual confounding on the observational side (PMID 19528338). This judgment reflects the state of the data published up to February 2008 as of 2009.

Adding our own point to this: The degree to which the answers from the two designs diverged depended on the outcome variable. They diverged for mortality and did not diverge sharply for revascularization. This abstract does not explain why. However, neither "observational studies always exaggerate" nor "observational studies are just like trials" can be stated based on this table alone.

There are also examples where observational data failed to reproduce the answer from a trial. This is a pilot study that tried to mimic a single randomized trial using electronic health record data. Mimicking means selecting patients from medical records under the same conditions as the past trial and running the same comparison again. The mortality hazard ratio was 0.95 (0.78–1.16) in the emulation and 0.49 (0.38–0.64) in the original trial. The authors' conclusion is that this emulation result did not match the benchmark trial. They cite differences in treatment and data capture between the two populations, confounding by indication, treatment crossover, and the accuracy of diagnosis capture as reasons (PMID 39348118).

What this study was trying to measure was not the treatment effect but the performance of the data source, and the original trial's results were not refuted. There is one takeaway. When the same question is asked using two data sources, the answers can diverge, and the reasons for the divergence can be named one by one.

Then, when do non-randomized studies support valid inferences? A paper titled after this question gives five checklist questions (PMID 33826756). They are whether the design emulates a target randomized trial, whether the comparison group is appropriate, whether the primary analysis adjusts for measured confounding variables, whether sensitivity analyses quantify the impact of residual confounding, and whether the methods are auditable and, where possible, reproducible.

② "If the E-value Is Large, You Can Rest Easy"

The E-value is an intuitive and useful sensitivity analysis tool that turns arguments about unmeasured confounding into numbers (PMID 34190835). However, in the usage reality seen earlier, the median for 43 studies where authors judged that "confounding likely had an effect" (1.88) and the median for 348 studies where they judged that "it likely did not have an effect" (1.82) practically overlapped (PMID 31930286). This means that opposite verdicts are reached given numbers of the same size. There is no universal cutoff value for interpretation to begin with, and biases other than confounding are not factored into this calculation (PMID 42264181).

Furthermore, E-values calculated after applying propensity score methods tended to become even larger when unobserved confounding caused the estimate to be biased further (PMID 38539082). In such situations, this means that the E-value may inaccurately represent the magnitude of the unobserved effect required to change the result.

The prescription offered by these same papers is how to use the tool properly. It is to interpret findings by comparing them against the expected strength of confounding in each field (PMID 31930286), and to actually name plausible unmeasured confounding variables (PMID 42264181).

③ "Our Field Is Doing Fine"

The evidence in this article comes from specific samples in specific fields and does not represent "papers in general." Nor did we go looking for surveys reporting that "there were no problems." With that caveat, surveys from different fields produced results pointing in the same direction. Pharmacoepidemiology (PMID 39098826), critical care medicine (PMID 38012221), propensity score literature (PMID 25433444), and cluster randomized trials (PMID 25648791) do so.

There is also a meta-epidemiological study in which two people independently scored 50 non-randomized clinical studies using 35 quality criteria (PMID 36476329). Meta-epidemiology is research that measures research practices by using the papers themselves as data. The subjects were papers published from 2012 to 2018, and 49 of them were published in two general American medical journals.

Not a single study fully met all application criteria, and the average completion rate was 72% (±10%). The lowest categories were items adjusting for observed effects and items verifying them. Among items with a completion rate of 50% or lower were residual bias analysis (14%) and falsification tests for residual confounding (8%). A falsification test is an inspection that deliberately looks for signals that should appear if the result were wrong. This ratio did not change over time. The authors concluded that these items are concrete targets that researchers and editors can fix (PMID 36476329).

To Go Deeper

For all three tools, the fastest approach is to read the original source paired with an overview of limitations.

There are also gaps left empty by this article. One is the approach of designing and reporting observational studies from the start as if they were hypothetical randomized trials. One of the 21 items in a checklist published in 2025 connects directly to the topic of this article: it instructs researchers to report the results of sensitivity analyses regarding assumptions and design-and-analysis choices (PMID 40899949). Another is the principle of first deciding what you are trying to measure in a randomized trial and then tailoring the analysis to match, which was only briefly touched upon here (PMID 38825841).

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This branch covering confounding and adjustment concludes here. What is left behind is a single reading rule.

When you encounter the sentence "There may be unmeasured confounding," check whether or not that sentence is the final one. If it ends right there, that is not humility; it is incompleteness. If there are sentences that follow, there are three questions to ask. The first is whether they calculated how strong a confounder would need to be to wipe out this result. The second is whether they compared that value against the strength of confounding expected in this field. The third is whether they actually named the unmeasured confounding variable.

If this rule is read as "Do not trust observational studies," this article has failed. This literature did not stop at diagnosing the problem. It created designs that reduce confounding by indication, built tools to measure the magnitude of remaining confounding, and has even verified what that magnitude actually is using linked data. And the limitations of those tools are being reassessed within that same literature. None of these tools can measure unmeasured things in your place. However, readers can check whether the paper tells them which of those things were done.

Source Papers

E-value

• PMID 28693043 (2017) — Original paper. Definition and reporting recommendations.
• PMID 34190835 (2021) — Application example. Prenatal care ↔ low birth weight 1.45–5.63.
• PMID 41343587 (2025) — Cornfield + Monte Carlo. 0.08 explanation condition met in under 2% (under 6% for 0.25).
• PMID 42264181 (2026) — Overview. Absence of cutoff, failure to reflect other biases, selective reporting.
• PMID 31930286 (2020) — Actual usage (87 papers, 516 values). Median 1.88 (43), 1.82 (348), 2.02 (125).
• PMID 38539082 (2024) — Simulation. Caution needed when interpreting E-values after propensity scores.

Negative Controls

• PMID 20335814 (2010) — Original paper. Two types and detection conditions.
• PMID 38040387 (2024) — Scoping review (37 papers). Detection 14, calibration 16, adjustment 5.
• PMID 37851862 (2024) — Actual usage (184 papers). Detection 81%, calibration 9%. Many unverified assumptions.
• PMID 37338976 (2023) — Overview of limitations. Potential lack of specificity and sensitivity, inability to prove the null hypothesis.

Actually Measuring Residual and Unmeasured Confounding

• PMID 39098826 (2025) — Review (158 papers). Concern 93%, sensitivity analysis 53%.
• PMID 27091131 (2016) — Method guide.
• PMID 41708481 (2026) — Proof of principle. FDA Sentinel MGB linked data. Most claims proxy variables are balanced.
• PMID 42093129 (2026) — 500 simulated cohorts. Relative bias after adjustment ≈0.

Confounding by Indication

• PMID 19457638 (2010) — 1,798 breast cancer patients. 2.6 → restriction + regression 1.1, propensity score 1.3, instrumental variable 0.9. Neither controls it.
• PMID 26474974 (2015) — Review (23 papers). Adjustment increased estimates by 12%/9%/7%. Stop using non-specific outcome variable cohorts.
• PMID 35019190 (2022) — Core concept. Restriction by indication, active comparator.
• PMID 25800216 (2015) — Design. New user.

Propensity Scores

• PMID 29684154 (2018) — Primer. Four uses.
• PMID 28104076 (2017) — Comparison of four cohorts. Not necessarily superior to regression adjustment.
• PMID 40779360 (2025) — Overlap weighting. Present multiple methods together.
• PMID 25433444 (2015) — Reporting status (296 papers). Variable selection 34.4%, balance 59.8%.
• PMID 37481434 (2023) — Author guidelines. Requirement to state assumptions and limitations.
• PMID 34547404 (2022) — Practical guidelines. Items to report.

Covariate Adjustment in Randomized Trials

• PMID 41474130 (2026) — FDA 2023 guidance. Prespecified adjusted primary analysis is acceptable.
• PMID 41988813 (2026) — Overview. Power gains are modest.
• PMID 42285376 (2026) — 50 empirical studies. Variance reduction 13.3% and 4.6%. Concise regression.
• PMID 34454099 (2021) — Simulation. Changing direction reporting leads to up to 48% false declaration.
• PMID 25648791 (2015) — 300 cluster-randomized trials. 32% of 219 adjusted trials were prespecified.
• PMID 38825841 (2024) — Overview. Decide what you are trying to measure first.

Observational Studies and Randomized Trials Side by Side

• PMID 19528338 (2009) — Meta-analysis (22 randomized, 34 observational papers). Both designs show a decrease in revascularization.
• PMID 39348118 (2024) — EHR emulation. Discrepancy with benchmark trials. Data source performance evaluation, not effect adjudication.
• PMID 33826756 (2022) — Decision framework. 5 checklist questions.
• PMID 36476329 (2022) — Metascience (50 papers, 35 benchmarks). Average 72%±10%. Bias analysis 14%, falsification test 8%.
• PMID 38012221 (2023) — Critical care medicine (79 papers). All 5 target trial elements 38%, all 3 causal assumptions 9%.
• PMID 40899949 (2025) — TARGET guidelines. 21 items, including reporting of sensitivity analyses.