Some Studies Cannot Count Risk — The Design Picks the Measure, and Pooling the Strata Changes the Number

There is evidence that women with schizophrenia receive less breast cancer screening, develop breast cancer more often, and die from breast cancer more often. This is compared to women without schizophrenia or the general population. There has also been a long-standing suspicion that, among antipsychotics, drugs that raise a hormone called prolactin increase that risk. Therefore, a nationwide study was conducted in Finland. The researchers gathered women with a breast cancer diagnosis and women without one separately, and then looked backward to compare what drugs both groups had used in the past and for how long. A study design that gathers people in whom an outcome has already occurred and people in whom it has not separately and investigates the past is called a case-control study. This is the kind that asks currently sick people, "What have you done up until now?"

Among the women diagnosed with breast cancer, the odds of having been exposed to prolactin-raising drugs for more than 5 years were statistically significantly higher compared to exposure of less than 1 year. Odds are the value obtained by dividing the number of people in whom an event occurred by the number of people in whom it did not occur. There was no significant difference in drugs that do not raise prolactin.

A commentary that examined this study from the perspective of interpreting odds ratios does not deny the results themselves. However, the author concludes that readers cannot judge from this design and result whether drugs that do not raise prolactin have a lower risk of breast cancer than drugs that do raise it. And alongside the risk of breast cancer, since other side effects that accompany rising prolactin are well known, the author includes the sentence that avoiding or managing them is desirable (PMID 34813689).

There is a reason why this study reported "how many times the odds" rather than "how many times the risk." Risk cannot be counted in this design. Risk here is the proportion of people who experienced the event over a defined period.

The value obtained by dividing the odds of two groups is the odds ratio, and the value obtained by dividing the risk of two groups is the risk ratio. How the two values differ was covered in "An Odds Ratio Is Not a Risk Ratio — What the 'Times More Likely' Is a Multiple Of". This article covers two subsequent things. First, the design determines which metrics can be produced. Second, the odds ratio has one more property that other metrics do not have. Subgroups divided by a single criterion, such as age or body type, are called strata, and even if the odds ratio is the same for every stratum, the value changes when the whole is pooled together.

The new terms to learn are six, and they are defined where they first appear.

⚠️ The diseases, drugs, and figures appearing below are entirely examples to show how to read numbers. They are not judgments on which treatment is good or bad, and each number has meaning only within the design and subjects of that study.

The Design Determines the Metric

Here, the metric refers to a value that expresses the difference between two groups as a single number, such as a risk ratio or an odds ratio. What a study observed determines which metrics can be calculated in that study.

A Design That Follows Along and Counts — Cohort Studies and Randomized Trials

A cohort study is a design where people are divided in advance and followed over time to count the outcomes. For example, it is like watching 1,000 smokers and 1,000 non-smokers for 10 years and counting how many people get sick. If who goes into which group is left to chance like a coin toss, it becomes a randomized trial. Both designs can directly count the risk in each group. If 80 out of 1,000 people get sick, the risk is 8%.

Yet it is common for cohort studies and randomized trials to report odds ratios. There are few designs that actually require using odds ratios. The reason odds ratios are widely used lies in logistic regression. Logistic regression is a statistical model widely used for data where the outcome is divided into yes or no, and it outputs an odds ratio as the calculation result. The alternative is binomial regression, which directly calculates a risk ratio. In the example data from this paper dealing with a cohort where the outcome is common, the odds ratio inflated the risk ratio by more than double. The authors' conclusion is that logistic regression should be greatly reduced in cohort studies (PMID 12377421). This means that if only an odds ratio is reported in a cohort where the outcome is common, that value can make the effect look larger than it actually is.

Binomial regression has one weakness. There are cases where the calculation fails to reach the answer, in other words, fails to converge. A paper reviewing how to calculate risk ratios in studies that observe by following forward in time (prospective studies), such as cohort studies or randomized trials, notes first that consensus has been reached after a long debate in much of the literature that risk ratios should be preferred over odds ratios. The practical recommendation is log-Poisson regression with corrected standard errors, which is one of the risk ratio calculation methods used instead when binomial regression fails to converge. The caveat is also added that the risk of misreading an odds ratio must be checked especially when the outcome is common (PMID 26443254).

Randomized trials have one more odds ratio problem left. It is a problem that arises even when the two groups are perfectly balanced, and it is covered in the later section "4 in Each Stratum, Yet 3.4 Overall".

Counting at a Single Point in Time — Cross-Sectional Studies

A cross-sectional study is a design that surveys at a single point in time and counts "does this disease exist right now." Asking 2,000 students at a school today whether they have asthma is a cross-sectional study. What you can see with this design is only the proportion of people who have the disease at the moment of the survey, in other words, the prevalence. You cannot see new cases of the disease arising. Therefore, there are two candidates for indices to compare two groups. One is the prevalence ratio, which divides the prevalence of the two groups. The other is the prevalence odds ratio. The prevalence odds ratio is obtained by dividing the number of people who currently have the disease by the number who do not, and then dividing that value between two groups. When the prevalence is low, the two values are nearly identical, and as the prevalence gets higher, they diverge.

This difference actually appeared in a large-scale cross-sectional survey in Münster, Germany. For asthma, which has a prevalence of 7.8%, all estimates were similar. For wheezing (a whistling sound when breathing), which has a prevalence of 17.5%, the prevalence odds ratio yielded the largest value and the widest confidence interval. A confidence interval is the range where the true value is likely to lie, and the wider it is, the less precise the value means. Noting that cross-sectional studies frequently deal with common diseases, the authors recommend analyzing with a model that directly yields the prevalence ratio. If the calculation fails, they suggest adjusting the starting values (initial values) or using another calculation method called robust variance Poisson regression (PMID 15702210).

The Debate Over Indices for Cross-Sectional Data Is Not Over

There are opposing opinions to this recommendation to use the prevalence ratio, and the debate has not yet been settled on one side.

A paper addressing the problem of determining causality from cross-sectional data directly opposes the preference for prevalence ratios. The cumulative incidence ratio is the value obtained by dividing the proportion of people who developed the disease within a set period between two groups. The incidence rate ratio is the value obtained by dividing the speed at which new cases of the disease arise over the same time between two groups. According to this paper, when the conditions necessary to determine causality are met, the cumulative incidence ratio generally cannot be estimated by either the prevalence ratio or the prevalence odds ratio, and the prevalence odds ratio consistently gives a proper estimate of the incidence rate ratio. The conclusion is twofold. If those conditions do not hold, multivariable regression, which puts multiple factors in all at once, should be avoided entirely. If the conditions do hold, the most appropriate choice is logistic regression (PMID 20633293).

There is also a diametrically opposite conclusion. This is a paper that modeled changes in a group with chronic diseases using differential equations, examining the relationship between the prevalence odds ratio, the prevalence ratio, and the ratio of the speed at which new cases of the disease arise. In this paper's view, the prevalence odds ratio is difficult to interpret without restrictive assumptions. Furthermore, the prevalence odds ratio and the prevalence ratio can lead to different conclusions when judging confounding (where an association is inflated or reduced due to an external other factor) or effect modification (where the magnitude of an effect varies depending on a certain factor). The conclusion is that the prevalence ratio should be preferred because it is conservative, consistent, and interpretable (PMID 9624282).

The answers to the same question diverge completely. Therefore, there is one thing for readers to check: Does a paper that derives an odds ratio from cross-sectional data include a reason for that choice?

The Design That Counts Backwards — Case-Control Studies

Now we return to the design of the Finnish study that opened this primer: the case-control study. With this design, you cannot calculate the risk in each group. That is because the researcher decides how many cases (people who got the disease) and controls (people who did not get the disease) to include. If you double the number of controls, the "patient ratio" inside the study changes along with it. So that ratio is not the risk in the real population. The only ratio calculated directly in this design is the odds ratio. How that odds ratio estimates something is determined separately by how the control group was chosen.

A classic paper summarizing this situation states in its opening sentence that the term odds ratio is "technically correct but frequently misinterpreted." There are three ways to pick controls, and the value the odds ratio estimates differs for each way. If controls are chosen from person-time (the sum of all the time each person spent in a state where they could get the disease), that odds ratio estimates a rate ratio—that is, the ratio of the speeds at which events occur over the same time. If they are chosen from the population at risk at the start of follow-up, it estimates a risk ratio. If they are chosen from the survivors at the end of follow-up, it estimates an odds ratio. None of these three ways of choosing relies on the assumption that the disease is rare. Therefore, the authors recommend reporting both how the control group was chosen and what that "odds ratio" estimates (PMID 8144304).

Where the Rule That "It Is Fine If the Disease Is Rare" Is Actually Used

The rare disease assumption is the rule that "if a disease is rare, the odds ratio is close to the risk ratio." People often learn it this way. If a disease is rare, almost everyone is someone who did not get it, so the denominator of the odds (the number of people who did not get it) becomes almost the same as the total number of people. For a disease that 2 out of 100 people get, the odds are 2 divided by 98 and the risk is 2 divided by 100, making them practically the same value. The rule itself is correct. However, the place where this rule is needed is different from where people commonly think.

The rarity assumption is needed when you want to read an odds ratio as a risk ratio, but it is not needed when you want to read it as a rate ratio. This point was nailed down by a 1982 paper. Suppose that for each time a case gets the disease, a control is sampled from the risk set—the people who do not yet have the disease at that moment. An odds ratio obtained by matching this way converges to the true value (the incidence density ratio) as the sample size grows. This does not require the assumption that the disease is rare. An odds ratio calculated without matching is biased to one side if the proportion of exposed people is not constant throughout the study period. However, the authors add that as long as that proportion does not fluctuate wildly, the bias is negligible. The final sentence of the abstract deals with end-of-follow-up sampling, where controls are chosen at the end of the study. In this case, even if the disease is rare, if the exposed proportion is not constant, that odds ratio fails to properly estimate any value of interest (PMID 7124721). This means that the mere fact that a "rare disease" is present does not guarantee that an odds ratio from end-of-follow-up sampling estimates anything properly.

The Assumptions Real Papers Rely On

Here are the results of examining 150 case-control studies published in major general medical, epidemiological, and clinical specialty journals between 2001 and 2007.

• 125 papers (83%) collected newly developed cases. The source population from which the cases came is called the base population; among them, 102 papers (82%) were dynamic populations where people enter and leave, and 23 papers (18%) were fixed cohorts following only an initially defined set of people.
• Out of those 125 papers, 105 papers (84%) could interpret the odds ratio as a rate ratio. Among them, 57 papers (46%) required the base population to be stable for this. Stable means that the proportion of exposed people did not fluctuate wildly throughout the study period. The remaining 48 papers (38%) needed no assumptions at all, thanks to picking controls matched to the timing when cases occurred.
• Only 17 papers (14%) could interpret the odds ratio as a risk ratio, and 16 of those required the rarity assumption.
• 4 papers mentioned the rarity assumption, but in none of those papers was that assumption actually relevant. Not a single researcher mentioned the stable population assumption.

For the percentages in parentheses, only the first row has the total number of investigated papers as its denominator, while the rest have the number of studies collecting new cases as their denominator.

The authors' conclusion is this. What is needed to interpret an odds ratio is much more often a stable exposure distribution than a rarity assumption. And researchers almost never discuss what their odds ratio is estimating (PMID 18794220). The rule that "it is fine if the disease is rare" was largely different from the assumptions real papers actually relied on.

Simply matching controls to the time of disease onset does not fulfill all conditions either. Conditions summarized again in 2023 are as follows. A hazard ratio (instantaneous rate ratio) is the ratio between two groups of the speed at which events occur at a given moment. If the timing of control sampling was not separately controlled for, two things must be present together to be sufficient: the proportion of exposed people must not change over time, and the hazard ratio must not change over time. If the sampling time was controlled for, it is sufficient just that the hazard ratio does not change over time. The authors' recommendation is to critically evaluate all conditions used to interpret one's estimate in that way (PMID 37712381).

It Is 4 in Each Stratum but 3.4 Overall

An odds ratio has another property that follows it regardless of study design. Let us look at the numbers before the name. Imagine a randomized trial. The 400 participants are divided into two strata: people who rarely develop the disease and people who develop it easily. Let us assume the randomization was perfect, so the two strata went into the treatment group and control group in exact halves. The numbers below are made up for explanation, and the odds ratios are what we calculated directly from the numbers in each row.

In the first row, the odds for the treatment group are 50 to 50, which is 1, and the control group is 20 to 80, which is 0.25, and dividing them gives 4. The second row is 4 divided by 1, which is also 4. When we combine the two rows, the treatment group becomes 130 to 70 and the control group becomes 70 to 130, and the odds ratio drops to 3.4.

It was 4 in every stratum, yet the overall is not 4. 3.4 is lower than both strata, so it does not even lie somewhere between the two strata. There is no place to call it an average of the stratum-specific values. In the same table, the risk ratio moves differently. The first row is 50% and 20%, so it is 2.5 times. The second row is 80% and 50%, so it is 1.6 times. Combined, they are 65% and 35%, so it is about 1.9 times, and 1.9 lies between 2.5 and 1.6.

Non-collapsibility is the property where a value measured in the entire population does not become a simple average of the values measured in the individuals or subgroups that make up that population. The odds ratio in the table shows precisely this property. Conversely, an index where the overall value comes out as the average of the partial values is said to be collapsibly equal.

This property starts from the odds. The odds itself is non-collapsible, and the odds ratio amplifies the non-collapsibility of the odds even further. Non-collapsibility is different from confounding. The two are frequently confused, so a follow-up paper to the one addressing this property of the odds separately demonstrates the difference using numerical examples (PMID 34119647).

Confounding is when an association is inflated or reduced because of a third factor. Non-collapsibility happens purely through arithmetic even when there is not a single such factor. The preceding table is an example of that. Even though randomization placed the two strata into both groups in exact halves, combining the strata caused the odds ratio to drop.

Misconceptions in Practice — Assessing Confounding

A common misconception caused by this property lies in assessing confounding. Adjusting for a variable by including it in the calculation to strip away its effect is called adjustment. A widely used convention is to consider confounding present if the estimate changes by more than 10% before and after adjustment. However, applying this criterion to logistic regression can lead to wrong conclusions. As seen in the table earlier, this is because an odds ratio moves simply by adding and removing strata, even when there is no confounding.

When examined through simulation experiments, the difference between the two estimates before and after adjustment can either underestimate or overestimate the actual confounding bias. This means that the mere fact that the odds ratio changed before and after adjustment cannot be used to judge how much confounding there was. There are two prescriptions. First, variables to adjust for are determined by subject-matter knowledge at the design stage. Second, to measure the magnitude of confounding bias, the unadjusted estimate is compared with the estimate from an inverse probability-weighted model. Inverse probability weighting is a method that makes two groups comparable by weighting them with the inverse of the probability of being exposed (PMID 34225653).

Differences That Persist Even in Balanced Randomized Trials

The conditional effect is the effect with conditions like strata held constant, which is the effect applicable to a single patient right in front of a clinician. The marginal effect is the effect averaged across the entire population. In the table, the values calculated separately for each stratum are the conditional odds ratios, and the value calculated by combining the two strata is the marginal odds ratio. Using odds ratios makes the two differ even in a randomized trial where the baseline conditions are perfectly balanced.

How different the two odds ratios are depends on two things: how strongly the stratifying variable is associated with the outcome, and how that variable is distributed among the trial participants. Because risk ratios are not affected by noncollapsibility, the conditional risk ratio and the marginal risk ratio are the same when adjusting for a balanced variable. Therefore, the recommendation of the paper that provided this numerical example is twofold: that risk ratios be used more frequently in reporting randomized trials, and that when using odds ratios, adjustment should be considered even when variables are balanced (PMID 21195797).

It is a different story that the risk ratios in the previous table differed across strata as 2.5 and 1.6. That was a case where the effect itself differed across strata. The statement that a risk ratio is collapsibly means that if the risk ratios are the same across strata, combining them keeps that value unchanged. An odds ratio is not maintained when combined even if it is the same across strata.

The difference between conditional and marginal can even change the judgment of choosing a treatment. When effect modification and noncollapsibility are present, the treatment ranking given by conditional estimates and the treatment ranking given by marginal estimates can contradict each other. The two estimates answer different decision questions, and when effect modification is present, those questions no longer point in the same direction. The recommendation is to make a practical comparison of the two estimates in the target population where the decision will actually be made (PMID 41626969).

Whether the odds ratio of the case-control study that opened this article is also noncollapsible depends on how the controls were selected, and this article does not cover that far. Noncollapsibility leads to the final question: Can a value measured in one place be carried over and used in another? This is the axis of the ongoing debate over odds ratios.

Common Misconceptions Two

① "If a disease is rare, a case-control study's odds ratio is a risk ratio"

That is only half true. How controls are sampled determines what an odds ratio estimates, and that estimation does not rely on the rarity assumption. The rarity assumption becomes necessary only when treating that value as equal to another metric, namely a risk ratio (PMID 8144304, PMID 7124721).

② "Therefore, papers using odds ratios are lazy"

That is not true. In some designs, only the odds ratio can be calculated directly, and in some sampling methods, that odds ratio properly estimates a rate ratio (PMID 8144304). Even those who teach caution about odds ratios acknowledge this point. A primer concludes that the odds ratio remains an attractive statistic for epidemiologists as long as it is not used uncritically as an estimate of relative risk (PMID 10390080). Here, relative risk means the same thing as risk ratio.

In Addition — The Formula for Converting an Odds Ratio into a Risk Ratio

A formula for converting an odds ratio back into a risk ratio actually exists. Widely cited is a correction formula published in 1998. Plugging in the adjusted odds ratio and the event rate in the unexposed group (the proportion of unexposed people who experienced the event) yields an approximation of the risk ratio. The authors published this formula because when an outcome is common (exceeding 10%), the adjusted odds ratio no longer approximates the risk ratio. The more common the outcome becomes, the more the odds ratio overestimates the risk ratio when it is greater than 1, and underestimates it when it is less than 1 (PMID 9832001).

However, conversion comes at a cost. Converted values can have inaccurate confidence intervals (PMID 12377421). Furthermore, in the debate below, those opposed to replacing odds ratios criticize the conversion methods recommended by odds ratio proponents as being biased in the values themselves (PMID 34390790).

An Honest Unresolved Question — Should We Abandon the Odds Ratio?

There is still no agreed-upon answer to this question.

The Argument for the Odds Ratio — Transportability

Transportability is the property where the value of an effect measured in one place can be safely carried over and used as-is in another setting with different circumstances. If a value measured in a trial holds true even for different patients at a much higher risk, that index is transportable. Guideline writers always carry over trial results from other countries to their own patients. The difference in circumstances referred to in this debate is the difference in baseline risk. Baseline risk is the original event risk that people have when there is no treatment or exposure.

The argument from one camp goes like this. In clinical epidemiology, we should use the odds ratio instead of the risk ratio, and the reason is transportability. The odds ratio is independent of the baseline risk, whereas the risk ratio is not. They claim that by recalculating with the examples raised by the opposing side, they have reconfirmed the non-transportability of the risk ratio. They view that the two indices measure different things, and the numerical difference is a problem only when misunderstood. They also view non-collapsibility as an expected phenomenon when there are risk factors rather than confounders, not a bias. Furthermore, they write that the regression models that yield risk ratios (log link) and the use of risk ratios in meta-analyses are themselves problematic, as shown by the same examples. This passage directly targets the direct estimation recommendation that this article translated earlier. The conclusion is that the odds ratio should replace the risk ratio, but the final output should be converted into a risk ratio or risk difference (PMID 34380019).

The Counterargument — The Data Do Not Say That

A meta-analysis is an analysis that gathers multiple studies dealing with the same question and combines them into a single value, and the Cochrane Database is a collection of such analyses. The first rebuttal came from 40,243 meta-analyses in this database. In most meta-analyses, studies with lower baseline risks tended to show higher odds ratios. This result contradicts the core premise of the supporting camp that the odds ratio is independent of baseline risk. The conclusion is that replacement is not advisable at present, and that any index may not be transportable (PMID 34384876).

The second rebuttal re-examines 20,198 meta-analyses from the same database and then categorizes the errors in the opposing camp's argument into four points. The first is circular reasoning. They set up a model assuming that the odds ratio is constant, and then showed under that model that the odds ratio is transportable. Second, the conversion method they recommend is biased. Third, there are counterexamples of meta-analyses where the risk ratio is transportable and the odds ratio is not. Fourth, they did not consider the factors that determine which studies enter a meta-analysis.

However, the results measured directly by this paper do not take either side. The transportability of the odds ratio and the risk ratio depended on the situation. Therefore, the conclusion has two layers. The authors state firmly that the proposal to replace the risk ratio with the odds ratio relies on circular reasoning and is particularly misleading in meta-analyses and clinical guidelines. At the same time, they write that neither odds ratios nor risk ratios are universally transportable. The alternative is to report how effects vary depending on factors that change the magnitude of the effect, like baseline risk (effect modifiers). The final sentence states that understanding that variability is essential for patient-centered care (PMID 34390790).

What Changes and What Does Not When You Change the Index — And a Reconciliation Proposal

Even if you change the index, the conclusions remain almost the same, and what changes are the results of testing for inconsistency and bias among studies. This is the result of re-analyzing 235 meta-analyses (147 reviews) using three indices: the odds ratio, risk ratio, and risk difference. The risk difference is the value obtained by subtracting the risk of the two groups. The value measuring inconsistency between studies was lowest for the odds ratio (median 42%). It was 5.1 percentage points higher for the risk ratio and 15.0 percentage points higher for the risk difference. Tests looking for bias in small studies were most frequently significant for the risk ratio (32%). It was 29% for the risk difference and 24% for the odds ratio. And the conclusion of whether an effect is statistically significant hardly changes. (PMID 25666885).

There is also an old proposal that summarizes this debate. A paper comparing the three indices first points out three things. Unless there is extreme extrapolation where values are drastically stretched beyond the range where data exist, the three models generally yield only small numerical differences. Risk difference and relative risk models can predict impossible event rates that are negative or greater than the total. And each index has theoretical justification. The proposal made after that is as follows. Risk difference and relative risk may have advantages in communicating risk, while odds ratios may be preferred for data analysis. The two purposes must be clearly distinguished, and different indices may be needed for each (PMID 11004419).

To Go Deeper

When you encounter an odds ratio in a paper, there are three things to ask.

1. What is the design? If it is a case-control study, the risk for each group cannot be counted, so what is calculated directly is the odds ratio. If it is a cohort or a randomized trial, the risk ratio could have been estimated directly, and it may be that they did not do so (PMID 12377421).
2. What does the odds ratio estimate? If it is a case-control study, where the controls were drawn determines that (PMID 8144304). If it is cross-sectional data, see if a reason for choosing the odds ratio is attached (PMID 20633293).
3. If the value changed before and after adjustment, is that confounding? (PMID 34225653). There are also attempts to reframe the indicator debate into a different framework, but this article does not go that far.

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An odds ratio is not a wrong number. It is a number that measures something different. And choosing that number is usually due to the design, not the author's sincerity. It is enough to remember a single table where the value is 4 in each stratum but 3.4 overall. That single page changes the way you read sentences like "the value changed after adjustment," and also explains why debates never end. Next time you encounter an odds ratio in an abstract, you will look at the design before the value.

Source Papers

Design and Metrics

• "…directly estimate risk ratios in cohort studies of common outcomes." (2002) — PMID 12377421 — In cohorts with common outcomes, odds ratios can severely overestimate risk ratios. Conversion methods can produce inaccurate confidence intervals, so direct estimation via binomial regression is recommended.
• "…Adjusted Risk Ratio in Prospective Studies." (2015) — PMID 26443254 — The preference for risk ratios was agreed upon after debate in a significant portion of the literature, and log-binomial models can suffer from convergence failure. The recommendation is robust error variance log-Poisson.
• "…effect estimates in cross-sectional studies." (2004) — PMID 15702210 — Münster cross-sectional study. Asthma (7.8%) showed similar estimates, while wheezing (17.5%) showed prevalence odds ratios with the maximum value and width. Since common diseases are frequently handled, use log-binomial, or starting-value adjustment or robust variance Poisson upon failure.
• "…appropriateness of the prevalence odds ratio…" (2010) — PMID 20633293 — Advocating for the prevalence odds ratio. Cumulative incidence cannot be estimated in either direction, and the prevalence odds ratio consistently yields the incidence density ratio. Avoid regression if assumptions fail, and use logistic if they hold.
• "Prevalence odds ratio or prevalence ratio…" (1998) — PMID 9624282 — Opposing conclusion. The prevalence odds ratio is difficult to interpret without restrictive assumptions and can yield different conclusions in confounding and effect modification. The prevalence ratio is preferred because it is conservative and consistent, and multivariable estimation should use generalized linear models or proportional hazards regression.

Case-Control Studies and Rarity

• "What does the odds ratio estimate in a case-control study?" (1993) — PMID 8144304 — Its opening sentence states that it is "technically correct but frequently misunderstood." Depending on control sampling (incidence density / risk set / survivors at the end), rate ratios, risk ratios, and odds ratios are estimated, and none of them depend on the rare disease assumption.
• "On the need for the rare disease assumption…" (1982) — PMID 7124721 — The matching estimator for incidence density sampling is a consistent estimator and the rare disease assumption is not needed. The unmatched estimator is biased if the exposure rate is not constant, but it is negligible unless the variation is large. Final sentence: Even if a disease is rare, if the exposure rate is not constant, the cumulative sampling odds ratio fails to consistently estimate any value.
• "What do case-control studies estimate?…" (2008) — PMID 18794220 — Survey of 150 papers (2001–2007). Among 125 incidence case studies (83%; 102 dynamic, 23 fixed), 105 (84%) allow a rate-ratio interpretation (57 require a stable population, 48 do not), while 17 (14%) allow a risk-ratio interpretation. Of the 4 mentioning rarity, the assumption was irrelevant, and no one mentioned the stable population assumption.
• "…odds ratios as rate-ratio estimates…" (2023) — PMID 37712381 — Sampling the risk set at the time of disease onset alone is not enough. Without time control, invariance of exposure prevalence over time + time-invariance of the hazard ratio are sufficient; with control, time-invariance of the hazard ratio alone is sufficient.
• "…Limitations of the Odds Ratio…" (2021) — PMID 34813689 — Commentary. The original study reported that the breast cancer odds were significantly higher for prolactin-elevating drugs used for over 5 years and not significant for non-elevating drugs. The conclusion is that this design and result cannot be used to compare and judge the two drug groups, and that managing the side effects of prolactin elevation is desirable.

Noncollapsibility

• "Noncollapsibility… Part 2…" (2021) — PMID 34119647 — The odds ratio amplifies the noncollapsibility of the odds, and noncollapsibility is different from confounding (frequently confused). Part 1 showed the noncollapsibility of odds with numerical examples.
• "Noncollapsibility and its role…" (2021) — PMID 34225653 — Applying the 10% change criterion to logistic coefficients can be wrong. Multivariable regression and inverse probability weighting yielded different but both valid estimates. The recommendation is to design adjustment variables at the design stage.
• "…a plea for multivariable risk ratios." (2011) — PMID 21195797 — Even in a balanced randomized trial, conditional and marginal odds ratios can differ, and the difference depends on the strength of association and distribution between the stratification variables and the outcome.
• "Effect modification and non-collapsibility together…" (2025) — PMID 41626969 — Review. When both are present together, conflicting treatment rankings can emerge between conditional and marginal estimates. The recommendation is to compare the two in the target population; the only method that can yield both is multilevel network meta-regression.

Conversion and Debate

• "…correcting the odds ratio in cohort studies…" (1998) — PMID 9832001 — Correction formula. When outcomes are common (>10%), the adjusted odds ratio fails to approximate the risk ratio, overestimating when greater than 1 and underestimating when smaller.
• "The Odds Ratio is 'portable' across baseline risk…" (2022) — PMID 34380019 — Odds ratio support. The claim that the odds ratio should replace the risk ratio based on portability, viewing non-collapsibility as expected rather than bias. It also notes that log-link regression and the use of risk ratios in meta-analyses are problematic.
• "…Paper 2: Is the Odds Ratio 'portable'…?" (2022) — PMID 34384876 — Rebuttal 1. Across 40,243 Cochrane meta-analyses, studies with lower baseline risk tended to have higher odds ratios. Replacement is not to be recommended, and it is likely that no measure is portable. The proposal is to present conditional effects alongside baseline risk.
• "…Paper 4: Odds Ratios are far from 'portable'…" (2022) — PMID 34390790 — Rebuttal 2. Reinvestigation of 20,198 meta-analyses, finding four errors (circular reasoning, conversion method bias, counterexamples, and inclusion criteria). The empirical finding is that portability depended on the context. The conclusion is that the replacement proposal is particularly misleading for meta-analyses and clinical guidelines, and since neither measure is universally portable, effect variation should be reported.
• "Choice of effect measure for meta-analyses…" (2015) — PMID 25666885 — Reanalysis of 235 meta-analyses (147 reviews). Inconsistency across studies was lowest for the odds ratio (median 42%), and higher for the risk ratio (+5.1%p) and risk difference (+15.0%p). Even when converted to risk ratios, the observed effect changed by 3%. Conclusions of statistical significance almost never changed.
• "Choice of effect measure for epidemiological data." (2000) — PMID 11004419 — Comparison of three measures. Absent extreme extrapolation, they usually yield only small numerical differences, and risk difference and relative risk models can produce impossible event rates. The suggestion is to separate measures for analysis from those for communication.
• "…odds ratio as an approximation to the relative risk." (1999) — PMID 10390080 — Primer. As long as it is not uncritically used as an estimate of the relative risk, the odds ratio remains an attractive statistic for epidemiologists.