# Critical Appraisal of Randomized Controlled Trials in Veterinary Medicine


## Key Takeaways

- **Allocation Concealment and Blinding are Crucial for Internal Validity:** True randomisation requires both sequence generation and concealment to prevent investigator bias in assigning animals to treatment groups. Blinding of caregivers, outcome assessors, and analysts, where feasible, protects against detection bias in outcome measurement.
- **Intention-to-Treat (ITT) Analysis Preserves Randomisation Benefits:** ITT analysis includes all randomised animals in their assigned groups, regardless of protocol adherence, to maintain the exchangeability established by randomisation and estimate the effect of *assigning* treatment, which is generally more clinically relevant than per-protocol analysis.
- **Sample Size Justification is Essential for Interpreting Negative Results:** Underpowered trials cannot reliably detect clinically meaningful treatment effects, rendering negative results inconclusive. Reports must include a pre-specified primary outcome and a sample size calculation based on a clinically meaningful effect size to allow for proper interpretation of statistical significance.
- **Unit of Allocation Must Match Unit of Analysis to Avoid Errors:** In veterinary trials, particularly in production animals, if animals are randomised at the pen or herd level, the statistical analysis must account for this clustering effect (e.g., using multilevel models) to prevent inflated Type I error rates and overly narrow confidence intervals.
- **Applicability Requires Matching Trial Population and Setting to Clinical Context:** Results from trials conducted in purpose-bred animals, single centres, or referral hospitals may not directly translate to diverse clinical patient populations or general practice settings due to differences in disease severity, comorbidities, or available resources.
- **Reporting Guidelines Like CONSORT Aid Critical Appraisal:** Adherence to reporting standards such as CONSORT provides a structured framework for evaluating RCTs, highlighting essential elements like flow diagrams for attrition, clear outcome definitions, and blinding details, thereby facilitating the identification of potential biases.

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Randomized controlled trials (RCTs) occupy a privileged position in the hierarchy of clinical evidence, sitting above observational designs and below systematic reviews and meta-analyzes. That position reflects the capacity of random allocation to distribute both known and unknown prognostic factors evenly across treatment groups, which in turn permits causal inference about treatment effects. For the veterinary researcher, the practical question is not whether RCTs are valuable, but whether a given trial deserves to influence clinical decisions. This article provides a structured approach to appraising the internal validity and applicability of veterinary RCTs. It is written for researchers, residents, and clinicians who read trial reports critically and who may design trials of their own. The methods described apply across species, from companion animals to production livestock, though the reader should expect species-specific complications in blinding, outcome measurement, and unit of allocation.

Critical appraisal is distinct from reading for content. A content-focused reading asks what the authors found. An appraisal asks whether the finding is true, whether it is true for the population studied, and whether it can be extended to the patients or herds the reader manages. The appraisal proceeds through three linked judgments: the risk of bias in the trial's design and conduct, the precision and completeness of its statistical reporting, and the applicability of its results to a target population. Each judgment requires the reader to interrogate specific elements of the report instead of to rely on the authors' summary. Reporting guidelines such as the CONSORT statement, maintained by the EQUATOR Network, provide a map of the elements that should be present in a trial report, and their absence is itself informative [EQUATOR Network reporting guidelines](https://www.equator-network.org/).

## At a Glance

| Appraisal Domain | Key Question | Red Flag |
| --- | --- | --- |
| Allocation concealment | Could investigators have predicted group assignment before enrollment? | Sequence generation described without concealment method |
| Blinding | Were caregivers, outcome assessors, and analysts masked where feasible? | Blinding described only as "single-blind" without specifying who was masked |
| Primary outcome | Was a single primary outcome declared before analysis? | Multiple outcomes reported without adjustment or pre-specification |
| Sample size justification | Was the trial powered for a clinically meaningful effect size? | Negative result with no sample size calculation reported |
| Attrition | Were all randomised animals accounted for at analysis? | Per-protocol analysis without intention-to-treat comparison |
| Unit of allocation | Was the unit of randomisation the same as the unit of analysis? | Group-housed animals randomised individually but analyzed as individuals |
| Applicability | Do the trial animals, setting, and protocol match the target population? | Single-center trial in purpose-bred animals applied to clinical patients |

## The Logic of Randomisation and Its Failure Modes

Random allocation works because it makes treatment groups exchangeable at baseline. If the exchangeability holds, any difference in outcome at trial completion can be attributed to the intervention, to chance, or to differential loss of animals from the groups. The threat to this logic is not randomisation itself but the ways in which it can be subverted or undone. The most important subversion occurs before the first dose is given. If the person enrolling animals knows or can predict the next assignment, they can steer particular animals into particular groups. This is allocation concealment, and it is distinct from blinding. Concealment protects the random sequence, blinding protects the measurements taken after allocation. A trial can have perfect concealment and no blinding, or perfect blinding and no concealment. Both are needed for full protection against bias.

The second failure mode is the loss of exchangeability through attrition. Animals that drop out of a trial are rarely a random subset of those enrolled. If the intervention causes adverse effects that lead to withdrawal, the remaining animals in the treatment group are a selected sample of those who tolerated the intervention. Analysis restricted to animals that completed the trial, a per-protocol analysis, preserves this selection. An intention-to-treat analysis, which analyzes animals according to their assigned group regardless of protocol adherence, preserves the exchangeability created by randomisation at the cost of diluting the treatment effect. The two analyzes answer different questions. The intention-to-treat analysis estimates the effect of assigning the treatment, the per-protocol analysis estimates the effect of receiving it. For a veterinary trial, the intention-to-treat estimate is usually the more clinically relevant, because it reflects what happens when a treatment is offered to a population of patients, some of whom will not tolerate it or will not complete the course.

## Statistical Power and the Interpretation of Negative Results

A trial that reports no statistically significant difference between groups is not necessarily a trial that found no difference. It may be a trial that lacked the statistical power to detect a difference that was present. Power is the probability that a study will detect an effect of a given size, and it depends on the sample size, the variance of the outcome, and the chosen significance threshold. The veterinary literature has a documented problem in this area. A survey of small animal clinical trials published between 2005 and 2012 found that only 22% of 238 reports included a sample size calculation, and only 9% reported a confidence interval around the treatment effect [Type II error and statistical power in reports of small animal clinical trials](https://pubmed.ncbi.nlm.nih.gov/24739118/). Among trials with negative results, only 14% were sufficiently powered to detect a 25% relative difference in outcome, and only 39% could detect a 50% difference. The implication is direct: a negative result from an underpowered trial is uninformative, and the reader should treat it as such.

The remedy is not to demand that every trial be large enough to detect any conceivable effect. It is to demand that the trial declare, before enrollment, the smallest effect that would be clinically meaningful, and then to verify that the sample size was calculated to detect that effect. The reader should look for the primary outcome, the expected control event rate or mean, the target difference, and the power calculation itself. The absence of these elements is a reason to discount the trial's negative conclusions, not to discard the trial entirely. A well-powered trial with a negative result is a useful finding. An underpowered trial with a negative result is a wasted opportunity that may mislead.

## Blinding and Outcome Measurement

Blinding protects the integrity of outcome measurement. In veterinary trials, the possibilities for blinding are more varied than in human medicine, because the patient cannot report symptoms and the owner, the clinician, and the laboratory analyst may each hold different information. A trial can blind the owner to the treatment assignment, which matters when the outcome is a subjective owner assessment such as lameness score or quality of life. It can blind the clinician who administers the treatment, which matters when the intervention requires skill or when the clinician's expectations might influence concurrent care. It can blind the outcome assessor, which matters when the outcome requires a judgment such as radiographic scoring or histopathological grading. Each of these is a separate decision, and a trial report should specify which parties were masked and how the masking was maintained.

Some outcomes resist blinding. Surgical interventions, for example, cannot easily be blinded to the surgeon, though the outcome assessor can be masked to the procedure. In such cases, the reader should ask whether the outcome measure is objective enough to withstand the absence of blinding. A survival endpoint or a laboratory value is less susceptible to ascertainment bias than a subjective pain score. The appraisal question is not whether blinding was perfect, but whether the unblinded parties had the opportunity and the motivation to influence the outcome in a direction that favours one group.

## The CONSORT Framework as an Appraisal Scaffold

The Consolidated Standards of Reporting Trials (CONSORT) statement provides the most widely accepted template for appraising randomised trials in health research. Its 25-item checklist maps directly onto the decisions made during trial design and reporting, and it functions equally well as a critical appraisal instrument when the original protocol is unavailable. The [EQUATOR Network reporting guidelines library](https://www.equator-network.org/) hosts the current CONSORT extension documents, including those for cluster trials, non-inferiority designs, and pragmatic trials. For veterinary work, the REFLECT statement, also indexed there, modifies CONSORT for livestock and food animal research, where group housing, pen-level allocation, and production outcomes require additional reporting items.

A structured appraisal using CONSORT proceeds in three passes. The first pass examines title, abstract, and introduction to establish what the investigators claim to have tested. The second pass interrogates methods and results for internal validity. The third pass judges applicability to your clinical population. Each pass generates a decision: proceed, proceed with caution, or reject.

## Pass One: What Was Actually Tested

Begin by extracting the trial's stated objective and primary outcome from the abstract. Then compare this with the methods section. Discrepancies between the stated aim and the measured endpoint are common and often signal post hoc reframing. A trial that claims to evaluate analgesic efficacy but reports only sedation scores has changed its question mid-course.

Identify the unit of allocation. In companion animal trials this is usually the individual animal, but in production medicine it is frequently the pen, litter, or herd. The [WOAH terrestrial animal health standards](https://www.woah.org/en/what-we-do/standards/codes-and-manuals/terrestrial-code-online-access/) emphasize that group-level interventions in food animals create clustering effects that must be accounted for in both design and analysis. If the authors allocated by pen but analyzed by individual animal without adjusting for clustering, the reported confidence intervals are too narrow and the type I error rate is inflated.

Confirm that the control condition is appropriate. A placebo control establishes absolute efficacy, while an active control establishes comparative efficacy. Both are legitimate, but they answer different questions. A trial comparing a new drug to no treatment cannot tell you whether the new drug outperforms the current standard of care.

## Pass Two: Internal Validity Under Scrutiny

The second pass applies the core validity questions: randomisation method, allocation concealment, blinding, follow-up completeness, and analysis population. The [revised Cochrane risk of bias tool](https://pubmed.ncbi.nlm.nih.gov/31800745/) used in the single-visit revascularisation systematic review structures these judgments across seven domains, each rated as low, high, or unclear risk.

Randomisation method matters because inadequate methods introduce selection bias. A trial that randomises by alternation, date of admission, or owner surname has not achieved true random allocation. The sequence should be generated by a random number table, computer algorithm, or equivalent mechanism, and the allocation sequence should be concealed from the investigator enrolling animals. Central randomisation, sequentially numbered opaque sealed envelopes, or pharmacy-controlled allocation satisfy concealment. A published randomisation table in the appendix does not, because the sequence remains visible to enrolling staff.

Blinding protects the measurement of outcomes, not the allocation itself. The [evidence-based review of low-level laser therapy for hair regrowth](https://pubmed.ncbi.nlm.nih.gov/26690359/) appraised five randomised trials and found that sham devices were essential for credible blinding in device trials, since owners and investigators can otherwise infer allocation from the sensation of treatment. In veterinary trials, the owner, the attending clinician, the outcome assessor, and the statistician can each be blinded independently. A trial that blinds only the owner has not blinded the outcome assessment unless the outcome is owner-reported.

Follow-up completeness requires a flow diagram. Count the animals enrolled, randomised, treated, and analyzed. The difference between these numbers reveals attrition. The [survey of small animal clinical trials](https://pubmed.ncbi.nlm.nih.gov/24739118/) found that most published veterinary RCTs did not report a primary outcome, a sample size calculation, or confidence intervals, which means the reader cannot distinguish a truly negative result from an underpowered one. When more than 20% of randomised animals are lost to follow-up, the trial's conclusions are fragile regardless of the analysis method.

The analysis population determines what the results mean. Intention-to-treat analysis includes all randomised animals in their assigned groups, regardless of protocol deviations. Per-protocol analysis includes only animals that completed the trial as specified. Intention-to-treat preserves the benefit of randomisation and estimates the effect of assignment, while per-protocol estimates the effect of treatment received. The two approaches answer different clinical questions, and a trial that reports only per-protocol results has discarded the randomisation advantage.

## Pass Three: Applicability to Your Population

Internal validity is necessary but insufficient. A methodologically sound trial conducted in a population unlike yours may not inform your decisions. The [hierarchy of evidence within the medical literature](https://pubmed.ncbi.nlm.nih.gov/35909178/) places randomised trials above observational designs, but the same source cautions that individual study limitations must be assessed through meticulous critical appraisal before applying results.

Ask whether the trial population resembles your patients in species, breed, age, disease severity, and comorbidity burden. A trial that excluded animals with concurrent disease, enrolled only young healthy adults, or used a referral hospital population may not generalize to first-opinion practice. The [MSD Veterinary Manual](https://www.msdvetmanual.com/) provides species-specific baseline data on physiology and drug handling that can help you judge whether the trial's inclusion criteria created a population with different pharmacokinetic or pharmacodynamic responses than your patients.

The trial's setting also matters. A university teaching hospital with intensive monitoring capability may produce results that cannot be replicated in a busy first-opinion practice. The equipment, staffing ratios, and follow-up protocols in the trial may exceed what you can provide. Conversely, a pragmatic trial conducted in general practice may have weaker internal validity but stronger external validity for your setting.

## A Structured Appraisal Checklist for Veterinary RCTs

The following checklist condenses the CONSORT items into a veterinary-specific appraisal instrument. Each item is scored as adequate, inadequate, or unclear, and the scoring pattern identifies the dominant bias risk.

| Domain | Appraisal Question | Adequate Response | Common Bias Detected |
|---|---|---|---|
| Allocation | Was the randomisation sequence generated by a valid method? | Computer generator, random number table | Selection bias from predictable allocation |
| Allocation | Was the sequence concealed until animals were enrolled? | Central randomisation, sealed envelopes | Selection bias from investigator manipulation |
| Blinding | Who was blinded, and does this cover the primary outcome? | Owner, clinician, and assessor blinded where feasible | Detection bias in outcome measurement |
| Baseline comparability | Were prognostic variables balanced across groups? | Table of baseline characteriztics with no material imbalance | Confounding despite randomisation |
| Sample size | Was a sample size calculation reported with a named primary outcome? | Calculation with effect size, alpha, and power stated | Type II error in negative trials |
| Follow-up | Is a participant flow diagram provided? | Numbers at each stage with reasons for loss | Attrition bias |
| Analysis | Was intention-to-treat analysis performed or justified? | All randomised animals analyzed in assigned groups | Attrition and protocol deviation bias |
| Outcome reporting | Were all pre-specified outcomes reported? | Protocol or trial registration available for comparison | Selective outcome reporting |
| Clustering | Was the unit of allocation accounted for in analysis? | Multilevel model or cluster-adjusted estimates | Unit-of-analysis error in group-housed animals |
| Applicability | Do the trial population and setting match your clinical context? | Inclusion criteria and setting described in sufficient detail | Limited external validity |

Score the trial by counting inadequate responses. Zero to two inadequacies suggests a trial whose conclusions you can provisionally accept. Three to five inadequacies requires you to weigh the direction of each bias and judge whether the effect estimate is likely to be inflated or attenuated. More than five inadequacies means the trial cannot support clinical decisions, and you should look to systematic reviews or higher-quality trials instead.

The [ARRIVE guidelines 2.0](https://arriveguidelines.org/) complement this checklist when you are appraising the preclinical or translational evidence that often precedes veterinary RCTs. ARRIVE items cover experimental design, sample size estimation, randomisation, blinding, and outcome measures in animal research, and they provide a common language for judging the quality of the foundational studies that motivate clinical trials.

## Species and Setting Modifications

The checklist requires adjustment for species and production context. In companion animal trials, individual allocation and owner-reported outcomes are typical, and the main threats are attrition and unblinded assessment. In food animal trials, group allocation is the norm, and the main threats are clustering effects and the use of production outcomes that may not reflect individual animal welfare. The [American Veterinary Medical Association practice resources](https://www.avma.org/resources-tools) note that welfare outcomes in production settings often require behavioral or physiological measures that are more resource-intensive to collect than weight gain or feed conversion, and trials that omit these measures may miss important harms.

Equine trials frequently use small sample sizes and crossover designs, which introduce period and carryover effects that the checklist does not directly address. For crossover trials, add questions about washout adequacy and period effect testing. Exotic animal and wildlife trials rarely achieve adequate sample sizes for randomisation to balance prognostic factors, and the checklist should be applied with the understanding that feasibility constraints may force quasi-random allocation. In these cases, the appraisal should focus on whether the authors acknowledged the limitation and adjusted their conclusions accordingly.

## Recognized Failure Modes and Early Detection

The most consequential failure modes in veterinary RCTs are not exotic. They are failures of allocation concealment, attrition with differential loss between arms, and outcome measurement that drifts from the protocol. Each leaves a characteriztic trace that an appraiser can detect if they know where to look.

Allocation concealment failure is detected by examining whether the randomisation sequence was generated independently of the person enrolling animals. A trial that reports "animals were randomly assigned" without describing sequence generation, concealment mechanism, or implementation steps should be treated as suspect. The discriminating check is simple: could the enrolling clinician have known or predicted the next assignment? If the answer is yes, the randomisation has failed regardless of the sequence's statistical properties.

Attrition problems are detected by constructing a flow diagram from the report. Count animals at enrollment, after randomisation, at each scheduled assessment, and at analysis. The failure mode is differential attrition, where one arm loses more animals than the other, often because of adverse events or perceived non-response. The discriminating check compares the proportion lost and the reasons for loss across arms. If reasons differ systematically, the treatment effect estimate is likely biased.

Outcome measurement drift is subtler. It appears when the definition of the primary outcome changes between the protocol and the results, or when subjective scoring systems are used without demonstrated inter-observer reliability. Detection requires comparing the outcome definitions across the methods and results sections and checking whether the assessors were blinded to treatment allocation. The [ARRIVE guidelines 2.0](https://arriveguidelines.org/) specify the minimum information needed to make these checks, and their absence from a report is itself a finding.

## Common Appraisal Errors and Corrections

Less experienced appraisers frequently mistake statistical significance for clinical importance. A trial can report a statistically significant difference that is too small to justify a change in practice, particularly when the outcome is a laboratory variable instead of a patient-centerd endpoint. The corrective action is to examine the magnitude of the effect and its confidence interval, not the p value alone. The [reporting standards catalogued by the EQUATOR Network](https://www.equator-network.org/) include CONSORT extensions that require effect sizes and precision, and their use signals a report that supports this kind of scrutiny.

A second common error is treating a negative result as proof of no effect. As documented in a survey of small animal trials, negative results were frequently underpowered to detect moderate-to-large effect sizes, and most reports lacked the sample size calculations and confidence intervals needed to interpret them [Type II error and statistical power in reports of small animal clinical trials](https://pubmed.ncbi.nlm.nih.gov/24739118/). The corrective action is to ask what effect size the trial could have detected, not what it failed to find.

A third error is overgeneralising from a single trial to all patients. The hierarchy of evidence places RCTs above observational designs, but that hierarchy must be applied with attention to individual study limitations [Hierarchy of Evidence Within the Medical Literature](https://pubmed.ncbi.nlm.nih.gov/35909178/). The corrective action is to ask whether the trial population, intervention protocol, and outcome measures match the clinical question at hand.

## Limitations of the Evidence Base

The veterinary RCT literature has structural limitations that no amount of careful appraisal can overcome. Sample sizes are often small, funding is limited, and many clinically important questions have never been subjected to randomised evaluation. Systematic reviews in veterinary-relevant fields frequently find few eligible trials, and those that exist often show methodological weaknesses. For example, reviews of regenerative therapies and of single-visit endodontic procedures have identified only a handful of randomised trials, with the remaining evidence drawn from case reports and animal studies [Limited Evidence Suggests Benefits of Single Visit Revascularization Endodontic Procedures](https://pubmed.ncbi.nlm.nih.gov/31800745/), [Laryngeal Applications of Platelet Rich Plasma and Platelet Poor Plasma](https://pubmed.ncbi.nlm.nih.gov/34384663/).

Expert opinion still differs on several points. One is the weight to give to animal model data when human trials are unavailable. Another is whether underpowered trials should be published at all, or whether they mislead more than they inform. A third is the threshold for considering a body of evidence sufficient to change practice, particularly for conditions where placebo responses are large or spontaneous resolution is common.

## Escalation and Referral

Most critical appraisal can be completed by a single clinician with access to the full text and a reporting guideline. Escalation is warranted when the trial involves regulatory decisions, when the results will inform treatment protocols across a practice or hospital, or when the statistical analysis is beyond the appraiser's comfort zone.

Laboratory involvement is appropriate when the trial's outcome measures depend on assays, histopathology, or imaging that the appraiser cannot evaluate for validity. Specialist consultation is warranted when the clinical condition is outside the appraiser's species or discipline expertise, or when the trial's inclusion criteria and outcome definitions require field-specific knowledge to interpret.

Regulatory reporting obligations arise when a trial reveals a suspected adverse drug reaction, a product defect, or a safety signal that meets the reporting criteria of the relevant authority. These criteria vary by jurisdiction and species, and the [WOAH terrestrial animal health standards](https://www.woah.org/en/what-we-do/standards/codes-and-manuals/terrestrial-code-online-access/) provide international reference points for surveillance and reporting expectations. The [AVMA practice resources](https://www.avma.org/resources-tools) can help identify applicable professional obligations in the United States, but the specific requirements of the relevant regulatory body must be consulted directly.

| Observation | Likely cause | Discriminating check |
|---|---|---|
| No allocation concealment described | Randomisation may be predictable | Look for separate sequence generation and enrollment personnel |
| Unequal attrition across arms | Differential loss biases effect estimate | Compare reasons for loss by arm |
| Negative result with wide confidence interval | Underpowered trial | Calculate detectable effect size |
| Outcome definition differs between methods and results | Post hoc outcome switching | Compare protocol, registration, and report |
| Statistically significant but clinically trivial effect | Large sample, small effect | Examine effect magnitude and confidence limits |

## Frequently Asked Questions

### How do I appraise an RCT when the full protocol or raw data are unavailable?

Work with what the report discloses. Check whether the authors state a primary outcome, report a sample size calculation, and present confidence intervals around the treatment effect. A survey of small animal trials found that fewer than 1% of reports included all three elements, so their absence is common but should lower your confidence in the conclusions. When the protocol is missing, compare the methods section against the [CONSORT reporting standards](https://www.equator-network.org/) to identify what should have been disclosed. If the report omits allocation concealment or blinding details, contact the corresponding author. If they cannot provide the information, treat those domains as unclear risk of bias instead of assuming the worst.

### What can I do when the trial used a sham or placebo that is impractical in my clinical setting?

The sham procedure in the trial may have been more elaborate than anything you can replicate. Focus on whether the comparison answers your clinical question, not whether you can reproduce the sham exactly. If the trial compared surgery plus a placebo injection against surgery alone, you can still apply the result by comparing your surgical outcome against the trial's control arm. Consider whether the treatment effect is large enough that the sham's physiological effects would change your decision. For regenerative therapies such as platelet-rich plasma, preparation protocols vary widely between studies, so check whether the trial's protocol matches what your facility can deliver before applying the results.

### How do I judge whether a trial's outcome measures matter for my patients?

Ask whether the measured outcome is a true clinical endpoint or a surrogate. Hair count in a laser therapy trial may not predict owner satisfaction or quality of life. For painful or progressive conditions, prefer trials reporting pain scores, time to recovery, or complication rates over those reporting only laboratory values. Check whether the trial measured outcomes at a clinically meaningful time point. A trial reporting radiographic changes at six weeks may not tell you what happens at six months. The [hierarchy of evidence](https://pubmed.ncbi.nlm.nih.gov/35909178/) ranks RCTs highly, but a well-conducted RCT measuring the wrong outcome still cannot answer your clinical question.

### How should I handle a trial with negative results when the sample size is small?

Treat negative results from small trials as inconclusive instead of as evidence of no effect. Calculate or estimate the power to detect a clinically meaningful difference. If the trial was underpowered, the confidence interval around the treatment effect will be wide and will usually include both no effect and a clinically important benefit. The survey of small animal trials found that most negative trials were underpowered even for moderate to large effect sizes. When you cannot calculate power yourself, look for the confidence interval and judge whether its upper bound excludes a benefit you would consider worthwhile. If it does not, the trial has not ruled out a useful treatment effect.

### How do I explain the limitations of an underpowered trial to a client or referring veterinarian?

Use plain language about uncertainty instead of technical terms. Say that the study was too small to detect a real difference if one exists, and that a negative result does not mean the treatment failed. Give the client a concrete sense of what the study could and could not show. For example, explain that the study would have detected a large improvement but could have missed a moderate one. Offer your reasoning for recommending or declining the treatment based on the totality of evidence, including other trials and your clinical experience. Reference the [ARRIVE reporting guidelines](https://arriveguidelines.org/) if the client asks why study quality varies, since these standards exist precisely to improve transparency in animal research.

### What records should I keep when I use an RCT to change my clinical practice?

Document the citation, the date you reviewed it, and the clinical question it answered. Record your assessment of the trial's internal validity and the population to which you intend to apply it. Note any differences between the trial population and your patient, such as breed, age, or disease severity, and state why you consider the results applicable despite those differences. Keep a brief note of the outcome measures you will use to judge whether the treatment works in your hands. This record supports later review of your own outcomes and provides a defensible basis for clinical decisions if questioned. The [AVMA practice resources](https://www.avma.org/resources-tools) offer guidance on documentation standards that apply to clinical decision-making.

## Related Clinical & Scientific Guides

* [Conducting Systematic Reviews of Veterinary Diagnostic Test Accuracy](/knowledge/veterinary-medicine/veterinary-research-methods/conducting-systematic-reviews-veterinary-diagnostic-test-accuracy)
* [Bias in Veterinary Research: Types, Sources, and Mitigation](/knowledge/veterinary-medicine/veterinary-research-methods/bias-veterinary-research-types-sources-mitigation)
* [Cluster Randomized Trials in Veterinary Research: Design and Analysis](/knowledge/veterinary-medicine/veterinary-research-methods/cluster-randomized-trials-veterinary-research-design-analysis)


## References and Further Reading

- [Low level laser therapy and hair regrowth: an evidence-based review.](https://pubmed.ncbi.nlm.nih.gov/26690359/). 2016.
- [Limited Evidence Suggests Benefits of Single Visit Revascularization Endodontic Procedures - A Systematic Review.](https://pubmed.ncbi.nlm.nih.gov/31800745/). 2019.
- [Hierarchy of Evidence Within the Medical Literature.](https://pubmed.ncbi.nlm.nih.gov/35909178/). 2022.
- [Laryngeal Applications of Platelet Rich Plasma and Platelet Poor Plasma: A Systematic Review.](https://pubmed.ncbi.nlm.nih.gov/34384663/). 2024.
- [Improving outcomes in hernia repair by the use of light meshes--a comparison of different implant constructions based on a critical appraisal of the literature.](https://pubmed.ncbi.nlm.nih.gov/17180568/). 2007.
- [Type II error and statistical power in reports of small animal clinical trials.](https://pubmed.ncbi.nlm.nih.gov/24739118/). 2014.
- [ARRIVE Guidelines 2.0 for Reporting Animal Research](https://arriveguidelines.org/). PLOS Biology, 2020.
- [EQUATOR Network Reporting Guidelines](https://www.equator-network.org/). EQUATOR Network.
- [MSD Veterinary Manual, Professional Edition](https://www.msdvetmanual.com/). MSD Veterinary Manual.

## Related Articles

- [Appraising Diagnostic Accuracy Studies in Veterinary Medicine](/knowledge/veterinary-medicine/veterinary-research-methods/appraising-diagnostic-accuracy-studies-veterinary-medicine)
- [Assessing Risk of Bias in Veterinary Randomized Trials](/knowledge/veterinary-medicine/veterinary-research-methods/assessing-risk-bias-veterinary-randomized-trials)
- [Cluster Randomized Trials in Veterinary Research: Design and Analysis](/knowledge/veterinary-medicine/veterinary-research-methods/cluster-randomized-trials-veterinary-research-design-analysis)
- [Critical Appraisal Tools for Veterinary Research: A Comparative Review](/knowledge/veterinary-medicine/veterinary-research-methods/critical-appraisal-tools-veterinary-research-comparative-review)
- [Equivalence and Non-Inferiority Trials in Veterinary Medicine](/knowledge/veterinary-medicine/veterinary-research-methods/equivalence-non-inferiority-trials-veterinary-medicine)

> 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.