# Risk Factor Analysis for Disease in Animal Populations


## Key Takeaways

- Study design selection (cross-sectional, case-control, cohort) is critical and driven by disease frequency, temporal relationships, and resource availability, directly impacting the strength of causal inference.
- Rigorous definition of both disease outcomes (using explicit diagnostic criteria and validated tests with known sensitivity/specificity) and exposures (ensuring independence from outcome knowledge and using validated instruments) is paramount to avoid misclassification bias.
- Multivariable modeling, particularly logistic regression for binary outcomes, is essential for estimating independent effects of exposures while controlling for confounders identified through causal diagrams (DAGs), not solely relying on automated stepwise selection.
- Confounding, where a third variable is associated with both exposure and outcome (e.g., breed influencing both brachycephaly and respiratory disorders), must be addressed through adjustment or stratification, guided by DAGs to avoid adjusting for mediators or colliders.
- Model validation, including internal methods like bootstrapping and external validation in different populations, is crucial to assess generalizability and prevent overfitting, especially when dealing with limited events per variable.
- Reporting standards, such as STROBE-Vet, are vital for transparency, requiring documentation of variable selection, unadjusted and adjusted estimates, model discrimination/calibration, and clear articulation of the target population for generalization.

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Risk factor analysis identifies characteriztics, exposures, or conditions that are statistically associated with the occurrence of disease in animal populations. It is a core activity of veterinary epidemiology, used to generate hypotheses, inform surveillance design, and guide preventive medicine. This article covers the design and analysis of observational studies for risk factor identification, with emphasis on variable selection and multivariable modeling. It is written for veterinary researchers and graduate students who need a practical framework for planning, executing, and interpreting such studies. The content is cross-species and does not address specific diseases or intervention trials.

The central question a risk factor analysis answers is deceptively simple: which factors distinguish affected from unaffected animals, and how strong are those associations? The answer depends on study design, sampling strategy, measurement quality, and the statistical methods used to separate genuine signals from confounding and chance. A poorly designed risk factor study can produce associations that are statistically significant but biologically meaningless, or worse, that misdirect control efforts. The principles described here follow the epidemiologic standards published by bodies such as the [CDC Principles of Epidemiology in Public Health Practice](https://www.cdc.gov/csels/dsepd/ss1978/index.html) and the [WOAH animal health surveillance standards](https://www.woah.org/en/what-we-do/animal-health-and-welfare/disease-data-collection/).

## At a Glance

| Parameter | Decision or Fact |
| --- | --- |
| Study designs | Cross-sectional, case-control, cohort, choice driven by disease frequency, time, and resources |
| Primary outcome | Disease status, defined by explicit diagnostic criteria applied uniformly |
| Exposure measurement | Must be independent of outcome knowledge, use validated instruments where available |
| Sample size | Calculated a priori for the smallest effect worth detecting, with allowance for attrition |
| Variable selection | Directed acyclic graphs or causal diagrams before modeling, avoid automatic stepwise selection alone |
| Multivariable methods | Logistic regression for binary outcomes, classification trees for interaction exploration |
| Model validation | Internal validation via bootstrapping or split-sample, external validation where possible |
| Reporting | Follow STROBE-Vet guidelines for observational studies in veterinary medicine |

## Study Design Logic

The choice of study design determines what inferences are possible. Cross-sectional studies measure exposure and disease at the same time, which makes them efficient for generating hypotheses but weak for establishing temporal sequence. Case-control studies sample affected and unaffected animals and compare past exposures, they are efficient for rare diseases but vulnerable to recall and selection bias. Cohort studies follow disease-free animals forward in time and provide the strongest observational evidence for causation, yet they are expensive and impractical for diseases with long latent periods.

An example of design trade-offs appears in feline hemoplasma research. A cross-sectional study of 713 Swiss cats identified associations between infection and male sex, outdoor access, and older age, but the design could not determine whether these factors preceded infection or arose from shared environmental exposure [Prevalence, risk factor analysis, and follow-up of infections caused by three feline hemoplasma species in cats in Switzerland](https://pubmed.ncbi.nlm.nih.gov/16517884/). A cohort design would be required to establish temporality, but the low prevalence of some infections would demand a very large sample.

For rare outcomes, case-control designs are often the only feasible option. A study of diabetes mellitus in dogs used records from the Veterinary Medical Data Base, matching 6,707 diabetic dogs to controls from the same teaching hospitals and years, and identified age, body weight, and sex as risk factors [Time trends and risk factors for diabetes mellitus in dogs: analysis of veterinary medical data base records (1970-1999)](https://pubmed.ncbi.nlm.nih.gov/12672370/). The use of existing records made this design practical, but it also introduced reliance on the completeness and accuracy of clinical coding.

## Defining the Outcome and Exposures

Disease definition precedes all other design decisions. The case definition must be explicit, repeatable, and applied identically to all study animals. For clinical outcomes, this may require combining history, physical examination, and laboratory findings into a scoring system. For infectious diseases, diagnostic tests with known sensitivity and specificity are preferred, and the implications of misclassification should be considered in sample size calculations.

Exposure variables must be defined with equal rigor. In questionnaire-based studies, the wording of questions, recall period, and response categories all influence measurement error. A study of feline diabetes mellitus used a convenience-sampled questionnaire and found that male sex, neutering, inactivity, body weight of 5 kg or more, and prior corticosteroid treatment were significant risk factors in univariate analysis [Feline diabetes mellitus in the UK: the prevalence within an insured cat population and a questionnaire-based putative risk factor analysis](https://pubmed.ncbi.nlm.nih.gov/17392005/). The authors acknowledged that owner-reported activity levels and body weight were subject to recall bias, and that the convenience sample limited generalizability.

## Confounding and Causal Structure

Confounding occurs when a third variable is associated with both the exposure and the outcome, creating a spurious association or masking a real one. Age, sex, breed, and management system are common confounders in veterinary studies. For example, breed is associated with both body conformation and the risk of upper respiratory tract disorders, so any analysis of brachycephaly and respiratory disease must adjust for breed or stratify by it. A study of dogs attending primary-care practices in England used multivariable logistic regression to compare extreme brachycephalic breeds with moderate and non-brachycephalic breeds, adjusting for age and sex [Epidemiological associations between brachycephaly and upper respiratory tract disorders in dogs attending veterinary practices in England](https://pubmed.ncbi.nlm.nih.gov/26401338/).

Directed acyclic graphs (DAGs) are the preferred tool for making assumptions about causal structure explicit before analysis. A DAG maps the hypothesized relationships among exposures, outcomes, and potential confounders, and identifies which variables must be adjusted for and which must not. Adjusting for a variable that lies on the causal pathway between exposure and outcome, a mediator, can introduce bias instead of remove it. Similarly, adjusting for a collider, a variable caused by both exposure and outcome, can create spurious associations.

## Multivariable Modeling

Multivariable models estimate the independent effect of each exposure while holding other variables constant. Logistic regression is the standard approach for binary outcomes, producing odds ratios with confidence intervals. Model building should proceed from the causal framework established in the DAG, not from automated variable selection alone. Stepwise procedures that rely solely on statistical significance can exclude important confounders or include variables that are merely correlated with the outcome.

Classification trees offer an alternative or complement to regression when interactions are suspected. A tree-based model of feline diabetes risk identified sex as the most important overall factor, with physical activity the next most important for females and breed the next most important for males [Feline diabetes mellitus in the UK: the prevalence within an insured cat population and a questionnaire-based putative risk factor analysis](https://pubmed.ncbi.nlm.nih.gov/17392005/). This type of analysis can reveal subgroups that a single regression model would miss, though trees are more prone to overfitting and require careful validation.

Model fit and calibration should be assessed after fitting. Hosmer-Lemeshow tests, area under the receiver operating characteriztic curve, and inspection of residuals are standard diagnostics. Internal validation through bootstrapping or split-sample approaches estimates how well the model will perform on new data. External validation, testing the model in a different population, is the strongest check but is rarely performed in veterinary studies.

## Model Building in Practice

### Variable Coding and Categorisation

The decisions made when coding variables shape every subsequent step of the analysis. Continuous exposures such as age, body weight, or herd size should be examined for linearity of association with the outcome before being entered into a model. A common approach is to fit the continuous variable and inspect the change in deviance against a model using restricted cubic splines or quartile indicators. If the relationship is non-linear, categorisation may be appropriate, but the choice of cut-points must be justified by biology or by the data distribution instead of convenience.

Categorical variables require a defined reference category. The reference should be the group with the largest number of events or the group that represents the baseline management state, because this provides the most stable estimates. Ordinal variables such as body condition score can be treated as continuous if the spacing between categories is clinically meaningful, but treating them as categorical avoids imposing an assumption of equal spacing that may not hold.

For production animal data, herd-level and animal-level variables must be coded separately and their hierarchical structure respected. A variable such as herd size may act differently at the herd level than at the animal level, and collapsing these levels loses information. The Swiss bovine viral diarrhea eradication program demonstrated that herd-level factors including herd size and early death rate were associated with the appearance of virus-positive newborn calves in previously unaffected herds, which illustrates the value of retaining the correct level of measurement [WOAH animal health surveillance standards](https://www.woah.org/en/what-we-do/animal-health-and-welfare/disease-data-collection/).

### Handling Missing Data

Missing data are the rule instead of the exception in veterinary records. The first question is whether the data are missing completely at random, missing at random, or missing not at random. Complete-case analysis is only valid under the first mechanism, and even then it reduces statistical power. Multiple imputation is preferred when the proportion of missing values is substantial and the missingness is related to observed variables.

In practice, a pragmatic sequence works well. Tabulate missingness for every candidate variable. If a variable is missing for more than 20 to 30 percent of records, consider whether it should be retained at all. If it is retained, examine whether the missingness is associated with the outcome. For example, in questionnaire-based studies of feline diabetes, owners of cats that died may be less likely to complete follow-up questions, which would bias the association between physical activity and disease [feline diabetes mellitus in the UK](https://pubmed.ncbi.nlm.nih.gov/17392005/). A missing indicator category can be used for categorical variables, but this approach can introduce bias if the missingness is informative. Multiple imputation with a model that includes the outcome and all candidate predictors is generally the more defensible choice.

### Collinearity and Variable Reduction

Before fitting a multivariable model, examine the correlation structure among candidate predictors. Two variables that measure the same underlying construct, such as body weight and body condition score, should not both enter the model unless their independent effects are of specific interest. Variance inflation factors above 10 indicate problematic collinearity, but lower thresholds of 5 are often used in smaller datasets.

The selection of variables for the final model should be driven by the study question. If the goal is prediction, automated procedures such as backward elimination with a liberal retention criterion of P < 0.10 or P < 0.20 are acceptable. If the goal is causal inference, variables must be selected based on the directed acyclic graph constructed during the design phase. Automated selection procedures cannot distinguish confounders from mediators, and their use in causal studies can produce estimates that are adjusted for variables that lie on the causal pathway.

A practical compromise is to fit a full model containing all variables identified from the causal structure, then use a change-in-estimate criterion to decide whether a variable is retained. A variable is considered a confounder if removing it changes the coefficient of the primary exposure by more than 10 percent. This approach preserves the causal interpretation while reducing the number of parameters in the final model.

### Model Diagnostics and Fit

After fitting the multivariable model, assess its performance before interpreting the coefficients. For logistic regression, the Hosmer-Lemeshow test compares observed and predicted event rates across deciles of predicted risk. A non-significant result supports adequate calibration, but the test has low power in small samples. The area under the receiver operating characteriztic curve summarizes discrimination, with values above 0.7 indicating acceptable separation of cases and non-cases.

In the analysis of upper respiratory tract disorders in brachycephalic dogs, multivariable logistic regression was used to quantify breed-type risk while accounting for age and sex, and the model provided prevalence estimates that differed substantially from crude comparisons [epidemiological associations between brachycephaly and upper respiratory tract disorders](https://pubmed.ncbi.nlm.nih.gov/26401338/). This illustrates why unadjusted breed comparisons can mislead when the age structure of breeds differs.

Influence diagnostics identify individual records that disproportionately affect the model. Standardized residuals, leverage values, and Cook's distance should be examined for the most extreme observations. A single influential record can change the direction of an association, particularly in studies with fewer than a few hundred events.

### Interpretation of Model Outputs

The odds ratio or hazard ratio from a multivariable model is conditional on all other variables in the model. This conditional interpretation differs from the marginal association observed in univariate analysis, and the two can diverge substantially when confounding is present. The 95 percent confidence interval communicates the precision of the estimate, and its width is determined by the number of events, not the total sample size. A study with 10,000 animals but only 30 events will produce wide intervals for all predictors.

For continuous predictors, report the effect per clinically meaningful increment instead of per one unit. A per-kilogram increase in body weight may be clinically negligible, whereas a per-5-kilogram increase is interpretable. The feline diabetes questionnaire study identified body weight of at least 5 kilograms as a risk factor, which is a threshold that owners and clinicians can apply directly [feline diabetes mellitus in the UK](https://pubmed.ncbi.nlm.nih.gov/17392005/).

### Reporting Standards

The final report should state the number of animals and events, the proportion of missing data for each variable, the variable selection procedure, and the criteria used for retention. Present both unadjusted and adjusted estimates so that readers can assess the impact of confounding. Report the model's discrimination and calibration, and describe the population to which the results can be generalized.

The [CDC principles of epidemiology in public health practice](https://www.cdc.gov/csels/dsepd/ss1978/index.html) emphasize that the interpretation of any association requires consideration of chance, bias, and confounding before causation can be considered. A statistically significant association from an observational study is a hypothesis-generating finding, not proof of causation. The Bradford Hill considerations, applied with appropriate caution, provide a structured way to evaluate whether the observed association is likely to be causal.

### Species and Production System Considerations

The correct analytical approach varies by species and production context. In companion animal practice, the unit of analysis is usually the individual animal, and data are often drawn from practice management systems. These data are subject to selection bias because the population attending clinics differs from the general population. The VetCompass approach, which samples from primary-care practices, provides a more representative frame than teaching hospital data, but still reflects the population that seeks veterinary care [epidemiological associations between brachycephaly and upper respiratory tract disorders](https://pubmed.ncbi.nlm.nih.gov/26401338/).

In production animal systems, the herd is often the unit of interest, and within-herd clustering must be addressed. Ignoring clustering produces standard errors that are too small and confidence intervals that are too narrow. Mixed-effects models with a random intercept for herd, or generalized estimating equations with an exchangeable correlation structure, are the standard approaches. The choice between them depends on whether the research question concerns herd-level effects or individual-level effects within herds.

The [WOAH terrestrial animal health code](https://www.woah.org/en/what-we-do/standards/codes-and-manuals/terrestrial-code-online-access/) provides the international framework for surveillance and reporting, and risk factor analyzes conducted for regulatory purposes must align with these standards. Studies intended to inform national control programs, such as the Swiss BVD eradication effort, require a different evidentiary standard than studies intended to generate hypotheses about disease mechanisms [bovine viral diarrhea eradication in Switzerland](https://pubmed.ncbi.nlm.nih.gov/21371766/).

### Common Failure Modes

| Failure mode | How to detect it | Consequence | Prevention |
| --- | --- | --- | --- |
| Overfitting | Events per variable below 10 | Unstable estimates, optimiztic discrimination | Restrict candidate predictors, use penalised regression |
| Residual confounding | Sensitivity analysis with additional covariates | Biased exposure estimate | Collect data on all known confounders at design stage |
| Misclassified outcome | Validation subset with gold standard | Biased odds ratios toward the null | Use objective diagnostic criteria, blinded outcome assessment |
| Selection bias | Compare included and excluded records | Spurious associations | Document the sampling frame, use weighted analysis |
| Clustering ignored | Intraclass correlation coefficient > 0.05 | Narrow confidence intervals, false positives | Fit mixed-effects models or use robust standard errors |

Each failure mode has a characteriztic signature in the data. Overfitting is suspected when the model performs well in the derivation dataset but poorly in validation. Residual confounding is suspected when the exposure coefficient changes materially after adding a covariate that was not in the original design. Misclassification of the outcome is often revealed by a sensitivity analysis that redefines the outcome using stricter criteria. Selection bias is detected by comparing the characteriztics of animals included in the analysis with those excluded. Clustering is quantified by the intraclass correlation coefficient, which estimates the proportion of total variance attributable to between-cluster differences.

The practical consequence of these failures is that the model's estimates do not reflect the true association in the target population. The remedy is always to return to the design phase and reconsider the sampling strategy, the measurement protocol, or the causal structure, instead of to adjust the statistical analysis after the fact.

## Recognized Complications and Early Detection

Risk factor studies fail in predictable ways. The most consequential failure is residual confounding, where an unmeasured variable distorts the exposure-outcome association despite multivariable adjustment. Detection relies on sensitivity analysis: refit the model with plausible additional covariates, use propensity scores or directed acyclic graphs to identify unmeasured common causes, and compare estimates across specifications. If the exposure coefficient moves materially, residual confounding is likely.

Selection bias arises when the study population differs systematically from the target population. In veterinary studies using hospital records, referral populations over-represent severe cases and certain breeds. The VetCompass approach, sampling from primary-care practice populations, reduces this bias relative to teaching hospital data. Detect selection bias by comparing the study sample's demographic structure with an independent census or surveillance source, and by examining whether inclusion criteria correlate with both exposure and outcome.

Measurement error in exposures collected retrospectively is common. Owner-reported management factors suffer recall bias, particularly when owners of affected animals search for explanations. Detect this by validating a subset of self-reported exposures against objective records, such as vaccination certificates or purchase receipts, and by comparing effect estimates between validated and unvalidated subsets.

Misclassification of the outcome produces bias toward the null when non-differential. Diagnostic tests with imperfect sensitivity or specificity, applied uniformly, attenuate true associations. Quantitative PCR assays for feline hemoplasmas illustrate the importance of assay performance: newly designed real-time PCR methods detected infections that earlier techniques missed, and risk factor associations differed between the three hemoplasma species. Assess outcome misclassification by testing a random sample of negative animals with a gold-standard method and by reviewing whether case definitions were applied consistently across study sites.

## Common Errors and Corrective Action

Less experienced analysts frequently dichotomise continuous variables at arbitrary cut points. This loses information and can create spurious associations. Corrective action: retain continuous predictors where biologically plausible, assess linearity with restricted cubic splines or fractional polynomials, and only categorise when a threshold effect is supported by the data or by prior evidence.

Overfitting occurs when the number of predictors is large relative to the number of events. A common rule is at least 10 events per predictor variable, though some authors recommend 15 to 20. Corrective action: reduce the candidate predictor set before modeling using prior knowledge, not univariate screening alone, and validate the final model with bootstrapping or cross-validation.

Stepwise variable selection, whether forward, backward, or bidirectional, is widely misused. It produces unstable models, biased coefficients, and standard errors that do not account for the selection process. Corrective action: prespecify the model based on causal reasoning, use stepwise procedures only for exploratory purposes, and report the full model-building pathway.

Univariate screening to select candidates for multivariable modeling, using a P-value threshold such as 0.2, can exclude important confounders that are not individually associated with the outcome. Corrective action: include variables that are known confounders from the literature even if univariate P-values are non-significant, and use change-in-estimate criteria instead of significance testing for confounder retention.

## Limitations of Current Evidence

The veterinary risk factor literature is dominated by cross-sectional and case-control designs, which cannot establish temporal sequence. Prospective cohort studies are rare because they are expensive and slow. The Swiss BVD eradication program demonstrates the value of population-level data collected during control campaigns: risk factor analysis using surveillance data identified herd-level predictors of virus-positive calves, including herd size and early death rate, that would be difficult to study prospectively.

Evidence for many risk factors rests on single studies or on studies from one region or production system. Feline diabetes risk factors identified in insured UK cats, including Burmese breed, male sex, neutering, inactivity, and corticosteroid treatment, may not generalize to other populations. Similarly, breed-associated upper respiratory tract disorders in English dogs reflect breed popularity and genetic background in that country. Extrapolation across countries, management systems, and genetic lines requires caution.

Expert opinion still differs on several points. The role of retrovirus coinfection in feline hemoplasma disease remains contested, the Swiss study found no association with retrovirus infection, whereas other authors have reported such associations. Whether subclinical infections should be treated, and whether risk factor findings should drive screening programs, depends on local prevalence and resources.

## Referral, Consultation, and Reporting

Statistical consultation is warranted when the analysis plan involves complex modeling, hierarchical data structures, or sparse events. Veterinary epidemiologists or biostatisticians should be engaged before data collection, not after analysis has stalled. Laboratory involvement is required when diagnostic assays are being developed or validated, as assay performance directly affects risk factor estimates.

Regulatory reporting obligations vary by jurisdiction and disease. The World Organization for Animal Health maintains international standards for disease notification and surveillance, and the Terrestrial Animal Health Code specifies which diseases must be reported to the organization. Veterinarians conducting risk factor research on notifiable diseases should confirm reporting requirements with their national veterinary authority before commencing work. The WOAH animal health surveillance standards describe the framework for such reporting.

The following table summarizes common problems and their discriminating checks.

| Observation | Likely cause | Discriminating check |
|---|---|---|
| Exposure coefficient changes when covariates added | Confounding | Compare crude and adjusted estimates, inspect directed acyclic graph |
| Effect estimate differs from published studies | Selection bias or different population | Compare study demographics with independent census data |
| Wide confidence intervals | Sparse events or collinearity | Check events per variable, examine variance inflation factors |
| Model unstable across bootstrap samples | Overfitting | Perform internal validation, reduce predictor set |
| Exposure effect disappears after validation subset analysis | Measurement error | Compare validated and unvalidated exposure subsets |
| Stepwise selection yields different models on resampling | Unstable variable selection | Prespecify model, use change-in-estimate for confounders |

## Frequently Asked Questions

### How Many Animals Do I Need to Study a Putative Risk Factor?

The required sample size depends on the expected effect size, the prevalence of the exposure, and the frequency of the outcome. For a rare outcome, a case-control design is more efficient than a cohort study. For a common exposure, you need fewer animals to detect a given odds ratio than for a rare exposure. Run a formal sample size calculation before data collection, specifying the smallest effect you consider biologically meaningful. Pilot data or published prevalence estimates, such as those from feline hemoplasma surveys, can inform these assumptions [Prevalence and risk factor analysis of feline hemoplasma infections in Switzerland](https://pubmed.ncbi.nlm.nih.gov/16517884/). Consult a statistician when the sampling design involves clustering, for example multiple animals per herd, because the effective sample size is smaller than the number of animals.

### What Can I Do When the Ideal Data Are Not Available?

Use the best available data and state its limitations explicitly. Electronic medical records from primary-care practice can support risk factor analysis when the data were not collected for research, as demonstrated in studies of brachycephalic dogs [Epidemiological associations between brachycephaly and upper respiratory tract disorders in dogs](https://pubmed.ncbi.nlm.nih.gov/26401338/). Validate the completeness of your exposure and outcome variables before modeling. If a key confounder was not recorded, consider proxy variables or restrict the analysis to a subgroup where confounding is less likely. Sensitivity analyzes can show how robust your conclusions are to missing information. When data quality is poor, a smaller, well-characterized prospective dataset may be more informative than a large, incomplete retrospective one.

### How Do Risk Factor Analyzes Differ Between Herd-Level and Individual-Animal Studies?

The unit of analysis determines the interpretation of every model coefficient. In herd-level studies, the outcome is typically herd status and exposures are management practices, biosecurity measures, or regional factors. Individual-level studies can identify host characteriztics such as breed, age, and sex, as shown in canine diabetes analyzes [Time trends and risk factors for diabetes mellitus in dogs](https://pubmed.ncbi.nlm.nih.gov/12672370/). Herd-level analyzes often require multilevel modeling to account for animals clustered within herds. The same exposure can have different effects at different levels, a phenomenon called ecological confounding. A factor associated with herd breakdown may not predict which individual animal becomes infected. State the level of inference clearly in the abstract and discussion.

### What Records Should I Keep During a Risk Factor Study?

Maintain a complete data dictionary from the first day of the study. Document every variable name, its coding scheme, the source of each value, and any transformations applied. Keep a log of all data cleaning decisions, including how outliers were handled and which records were excluded. Version-control your datasets and analysis scripts so that any result can be reproduced. Record the date of data extraction and the exact query used to define the outcome. For studies using clinical records, note how the diagnosis was confirmed and by whom. Good documentation also supports compliance with reporting standards and allows another researcher to replicate your analysis.

### How Do I Explain Risk Factors to a Client or Herd Owner?

Distinguish between a statistical association and a cause. Explain that a risk factor increases the probability of disease but does not guarantee it. Use absolute risk differences instead of odds ratios when possible, because odds ratios overstate risk when the outcome is common. For example, a breed that is 3.7 times more likely to develop diabetes still has a low absolute risk in most populations [Feline diabetes mellitus in the UK: prevalence and putative risk factors](https://pubmed.ncbi.nlm.nih.gov/17392005/). Frame recommendations around modifiable factors, such as vaccination status or housing, and acknowledge factors that cannot be changed, such as breed or age. Provide the owner with a written summary of the factors identified and the strength of the evidence behind each one.

### How Should I Handle Risk Factors That Differ Between Breeds or Production Systems?

Do not assume that a risk factor identified in one population applies to another. Breed, management system, and regional pathogen pressure can all modify associations. In the Swiss hemoplasma study, infection was associated with male sex, outdoor access, and older age, but these factors may not generalize to other countries or housing systems [Prevalence and risk factor analysis of feline hemoplasma infections in Switzerland](https://pubmed.ncbi.nlm.nih.gov/16517884/). When you analyze data from multiple breeds or systems, test for interaction terms before pooling. If interaction is present, report stratum-specific estimates instead of a single overall effect. In production animal medicine, consult the relevant international standards for surveillance definitions and reporting requirements [WOAH terrestrial animal health standards](https://www.woah.org/en/what-we-do/animal-health-and-welfare/disease-data-collection/).

## Related Clinical & Scientific Guides

* [Evaluating Veterinary Surveillance System Attributes](/knowledge/veterinary-medicine/veterinary-epidemiology/evaluating-veterinary-surveillance-system-attributes)
* [Network Analysis for Infectious Disease Spread in Animal Populations](/knowledge/veterinary-medicine/veterinary-epidemiology/network-analysis-infectious-disease-spread-animal-populations)
* [Randomized Controlled Trials in Veterinary Field Settings](/knowledge/veterinary-medicine/veterinary-epidemiology/randomized-controlled-trials-veterinary-field-settings)


## References and Further Reading

- [Prevalence, risk factor analysis, and follow-up of infections caused by three feline hemoplasma species in cats in Switzerland.](https://pubmed.ncbi.nlm.nih.gov/16517884/). 2006.
- [Epidemiological associations between brachycephaly and upper respiratory tract disorders in dogs attending veterinary practices in England.](https://pubmed.ncbi.nlm.nih.gov/26401338/). 2015.
- [Feline diabetes mellitus in the UK: the prevalence within an insured cat population and a questionnaire-based putative risk factor analysis.](https://pubmed.ncbi.nlm.nih.gov/17392005/). 2007.
- [Time trends and risk factors for diabetes mellitus in dogs: analysis of veterinary medical data base records (1970-1999).](https://pubmed.ncbi.nlm.nih.gov/12672370/). 2003.
- [Bovine viral diarrhea (BVD) eradication in Switzerland--experiences of the first two years.](https://pubmed.ncbi.nlm.nih.gov/21371766/). 2011.
- [Self-reported prevalence and risk factors of asthma among Korean adolescents: 5-year follow-up study, 1995-2000.](https://pubmed.ncbi.nlm.nih.gov/15479270/). 2004.
- [WOAH Animal Health Surveillance Standards](https://www.woah.org/en/what-we-do/animal-health-and-welfare/disease-data-collection/). WOAH.
- [CDC Principles of Epidemiology in Public Health Practice](https://www.cdc.gov/csels/dsepd/ss1978/index.html). CDC.
- [MSD Veterinary Manual, Professional Edition](https://www.msdvetmanual.com/). MSD Veterinary Manual.

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- [Sensitivity Analysis in Veterinary Disease Models](/knowledge/veterinary-medicine/veterinary-epidemiology/sensitivity-analysis-veterinary-disease-models)
- [Time Series Analysis for Veterinary Disease Surveillance](/knowledge/veterinary-medicine/veterinary-epidemiology/time-series-analysis-veterinary-disease-surveillance)
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> This article is educational professional reference material for veterinary audiences. It is not a substitute for veterinary diagnosis, individual clinical judgment, current product labeling, or applicable regulatory requirements.