兽研犬特应性皮炎（AD）是一种慢性炎症性和瘙痒性皮肤病，影响高达15%的犬，其临床表现受遗传、环境和微生物因素共同塑造。尽管国际动物过敏性疾病委员会（ICADA）确立了COSCAD作为核心结局指标集，为评估治疗效果提供了标准化的结局测量工具，但相比之下，决定试验结果有效性和可解释性的上游方法学考量所受到的关注相对较少。本叙述性综述采用结构化方法学框架，审视犬AD随机对照试验（RCT）中可能损害其质量的关键随机误差、偏倚、混杂和效应修饰来源。我们识别了试验设计中需要仔细控制的关键参数，包括食物和环境过敏原暴露、季节性、跳蚤感染、并发细菌和真菌感染、合并用药以及洗脱期的确定。本文分析了主要在未经治疗的中轻度疾病犬中开展的历史研究方案，以说明关键注册试验如何通过严格的病例定义、药物特异性洗脱间隔、合并用药限制以及严格的盲法和随机化来减轻这些误差来源。我们进一步审视了内部有效性与外部可推广性之间的权衡，以及在不断演变的治疗格局中传统解释性试验设计与真实世界可行性之间日益增长的张力。综合兽医皮肤病学专家组的多方视角，我们强调疾病严重程度、治疗史和治疗方式应如何指导入选标准、终点选择和评估时机。基于这些评估，我们指出了将标准化研究设计方法应用于如此异质性疾病所存在的局限性。将统一的方法学应用于如此异质的综合征，可能会掩盖疾病表现和治疗反应中具有临床意义的差异。进展需要灵活的、适合目的的研究设计，使关键方法学要素与所研究的表型相匹配，从而能够准确解读治疗效果并实现更有效的治疗开发。
引言
犬特应性皮炎（AD）是一种慢性炎症性和瘙痒性皮肤病，影响高达15%的犬，使其成为兽医临床上最常见和常治疗的疾病之一（1, 2）。犬AD的临床表现涵盖广泛的表现型谱，反映了多种致病因素之间复杂的相互作用（3）；临床表现受遗传易感性（如品种相关表型）、皮损分布（局限性 vs. 泛发性）、疾病阶段（急性发作 vs. 慢性）、表皮屏障缺陷以及皮肤菌群失调导致微生物感染或其他诱发因素的存在所塑造（4–6）。由于这种复杂性，许多犬需要多模式治疗方法，包括局部和全身治疗，以缓解瘙痒并消除与皮肤炎症相关的皮损（7–9）。
目前FDA批准用于治疗犬AD的全身性药物有四类。钙调神经磷酸酶抑制剂环孢素（Atopica，Elanco）是2003年首个获批用于治疗犬AD的免疫调节剂，随后环孢素口服溶液分别于2020年（Cyclavance，Virbac）和2023年（Modulis，CEVA）获批（10, 11）。近期，奥拉替尼（Apoquel，Zoetis）作为首个兽用Janus激酶（JAK）抑制剂于2014年问世（12）。第二种JAK抑制剂伊卢诺替尼（Zenrelia，Elanco）于2024年获得批准（13）。最近，兽医药品委员会（CVMP）于2025年对第三种高选择性JAK1抑制剂阿替维替尼（Numelvi，Merck）通过了正面意见（14）。首个由美国农业部（USDA）批准用于犬病的单克隆抗体（mAb）——抗白细胞介素（IL）-31的洛基维单抗（Cytopoint，Zoetis）（15, 16）于2017年上市。
尽管取得了这些进展，估计有10%至30%的犬治疗无效、复发和/或出现需要停用常规治疗的副作用（8, 17–19）。AD的多因素性质——以遗传、免疫和环境因素的多样性为特征——要求对新型治疗和患者亚组的研究采取细致且个性化的方法。因此，为推进犬AD治疗方案的开发并优化患者护理，需要能够捕捉这一复杂多因素疾病异质性的研究设计。
临床实践指南和叙述性综述已全面总结了犬特应性皮炎（AD）的治疗选择及 underlying 临床证据（7–9，20）。因此，本综述不旨在重复治疗建议或提供系统综述或荟萃分析，而是考察研究设计选择如何影响犬AD随机临床试验（RCT）的实施和解读。我们首先回顾为犬AD建立的主要终点，并考虑随机误差和系统误差如何扭曲观察到的关联，导致对真实治疗效应的高估、低估或逆转。然后我们分析历史RCT方案——主要在轻度至中度疾病的初治犬中进行——以说明早期研究如何设计以减轻这些误差来源。
研究选自同行评审文献，主要侧重于已发表的、支持FDA、USDA和/或EMA对当代犬AD全身治疗药物（包括oclacitinib、lokivetmab和ilunocitinib）监管授权的关键注册试验（补充表1）（15，16，19，21–24）。选择这些试验是因为它们为犬AD试验设计提供了既定的监管先例。相关试验通过公开的《信息自由法》摘要和相关监管文件确定，相应的同行评审出版物通过针对性PubMed检索找到。2006年至2025年的其他同行评审出版物通过补充PubMed检索确定，并评估其支持、限定或质疑本综述中提出的解释和建议的证据。由于这是聚焦的叙述性综述而非系统综述，检索并非旨在穷尽或支持证据确定性的正式分级。
最后，获取了七位兽医皮肤病学和临床试验设计专家的观点（见致谢），以将不同疾病严重程度和治疗环境下的方法学权衡置于背景中。专家由作者根据其在犬AD方面发表的专业知识和/或临床试验经验选定。通过虚拟圆桌会议使用结构化讨论指南征求输入，该指南涉及作者事先确定的方法学主题。作者记录并综合了反馈，并用于指导手稿的相关部分。这些观点为讨论研究设计方法如何需要适应疾病严重程度、治疗环境和预期治疗效应提供了信息。总体而言，它们强调了在异质性疾病中“一刀切”试验设计方法的局限性，这种方法可能掩盖不同患者亚组中具有临床意义的治疗信号。
为犬AD研究建立的终点
RCT是确定治疗干预效果的金标准，其主要目标是获得对患者结局治疗效应的有效且可量化的测量（25）。设计良好的RCT需要测量研究终点，以提供所测试干预措施的可靠信号。在犬AD等皮肤病中，评估疗效具有挑战性，因为缺乏疾病严重程度的客观实验室标志物（26–28）。为解决这一问题，国际动物过敏性疾病委员会（ICADA）建立了一套核心结局指标（COS），包括用于对犬AD皮肤病变和瘙痒严重程度进行分级的主观但经过验证的工具（COSCAD）（29，30）。
犬特应性皮炎范围和严重程度指数（CADESI）是一种复合评分指数，兽医皮肤科医生用于系统地对特应性犬的皮肤病变严重程度进行评分（31，32）。瘙痒视觉模拟量表（PVAS）是一种由主人评估的工具，用于评估瘙痒的严重程度（30，33）。因此，这些工具是犬AD RCT中最常用的主要终点（19，24，34，35）。为增强研究发现的深度和广度，研究者还可以纳入标准化的次要终点，如主人对治疗效果的总体评估（OGATE）和研究者的总体评估（2D-IGA）。纳入这些额外测量可加深研究见解，支持临床决策并指导未来研究（29）。
犬AD研究中的随机化、随机误差、偏倚、混杂和效应修饰
尽管已为犬AD建立了经过验证的终点，但仍需最小化随机误差（或机遇）和系统误差（或系统偏倚），以便对干预与结局之间的关系做出有效且精确的推断（36）。随机误差可定义为数据中因机遇而发生的自然波动，可影响几乎任何结局指标的精确性。另一方面，系统偏倚是指在研究设计、数据收集、分析和/或报告中引入的一致且可重复的误差，导致对干预真实效应的错误估计。系统误差可能增强、减弱或完全逆转真实治疗效应（37，38）。
在随机对照试验（RCT）中，通过随机化程序将受试者按机会分配到治疗组，可平衡可测量和不可测量的预后因素，从而提高各组在基线时具有可比性的可能性。若实施正确，随机化通过增强对观察到的结局差异归因于干预而非混杂变量的信心，从而加强因果推断。
随着样本量增加，随机化能更可靠地将与目标结局相关的变量分布到各治疗组，从而降低偶然失衡的风险。较大的样本量还可减少随机误差，从而获得更精确的效应估计和更窄的置信区间。然而，尽管随机化提高了组间平衡的概率，但在任何单项试验中都无法保证完美的可比性，尤其是当样本量较小时。例如，在一项比较口服抗组胺药 fexofenadine 与活性对照药甲泼尼龙的随机对照试验中，每组由15只犬组成的治疗组之间观察到瘙痒评分的基线失衡（39）。尽管 fexofenadine 并非犬特应性皮炎（AD）的当代标准疗法，但该研究提供了一个有用的方法学示例，说明小型兽医试验中可能出现偶然的基线失衡。此外，该研究报告的基线 CADESI 和瘙痒评分范围较宽，说明组内异质性较大可降低小研究人群中治疗效应估计的精确度。为减轻这些风险，研究者应纳入先验的样本量和把握度计算，并考虑适合研究规模和设计的随机化策略（例如，较小试验中采用区组随机化或分层随机化）。
鉴于随机化的局限性，可能需要额外的方法学保障措施来减少系统误差的影响。在犬 AD 研究中，若干因素可显著影响结局测量（例如，皮肤病变和瘙痒严重程度评分），必须在试验设计和实施中仔细考虑。已知可触发急性发作和/或改变犬 AD 临床特征的因素包括接触食物和环境过敏原、季节性以及并发皮肤感染和跳蚤感染（图1）。若未适当控制或考虑这些因素，可能引入偏倚或混杂，从而可能掩盖真实的治疗效果。以下总结了这些关键参数对犬 AD 结局指标的潜在影响，以及既往研究中如何处理这些因素。
[图：可能影响主要结局指标（CADESI 和]
在人类临床研究中已充分认识、在兽医临床试验中可能遇到的其他偏倚来源包括选择偏倚（纳入研究的动物与未纳入动物之间的系统性差异）、错分偏倚（各组间暴露或结局测量方式的系统性差异）、回忆偏倚（暴露或事件报告中的系统性误差）和失访偏倚（退出或排除的系统性差异）（表1）（40）。这些类别描述了可能扭曲组间比较有效性的系统性误差。
Table 1. Common sources of bias in canine atopic dermatitis clinical trials.
| Type of bias | Description | Illustrative example in a canine AD trial |
|---|---|---|
| Selection bias | Systematic differences between the characteristics of animals selected for the study and those not selected. | A trial recruiting only from referral dermatology practices may enroll dogs with more severe or treatment-refractory AD compared to the general population of atopic dogs, limiting generalizability of results |
| Misclassification bias | Systematic differences in how exposures, outcomes, or covariates are measured or classified between groups | In an unblinded trial, investigators aware of treatment allocation may systematically score CADESI-04 lesions more favorably in dogs receiving the investigational therapy than in those receiving placebo, leading to differential outcome assessment and inflation of the apparent treatment effect |
| Recall bias | Systematic differences in the accuracy or completeness of recalled information between groups | Owners of dogs experiencing more severe or recent atopic dermatitis flares may recall and report prior dietary exposures or environmental triggers differently than owners of dogs with milder disease, potentially creating spurious associations between reported exposures and disease severity |
| Attrition bias | Systematic differences in withdrawals or exclusions of animals from the study between treatment groups | Dogs experiencing inadequate response or adverse events may be more likely to withdraw from one treatment arm, leading to biased estimates of efficacy if missing data are not handled appropriately. For example, in the oclacitinib registration trial, more than 86% of placebo-treated dogs transitioned from the randomized comparison to an open-label study after Day 28, creating differential attrition that the authors noted biased longer-term between-group comparisons. |
| Performance bias | Systematic differences in care, management, or co-interventions between treatment groups apart from the intervention under study | Especially when blinding is incomplete, dogs in one treatment arm may receive more frequent follow-up visits, adjunctive topical therapies, or additional owner counseling than dogs in the comparator group, potentially exaggerating observed treatment effects |
动物、畜主和研究者之间的三元关系在兽医临床试验中引入了独特的方法学考量，影响入组、治疗实施、结局评估和研究保留。这种结构在人儿科和老年医学研究中的代理报告结局中有密切的类似情况（例如，父母代表幼儿报告（41），照护者代表认知障碍患者报告）。首先，犬AD试验通常使用畜主评估的PVAS以及研究者评估的CADESI。这些测量之间的不一致本身并不必然是偏倚的证据，因为它们评估的是在不同环境中捕获的疾病的互补表现：畜主在家庭环境中纵向观察瘙痒行为，而研究者在诊所就诊时评估炎症性皮肤病变。然而，任一测量内部的不一致性、评估者之间的变异，或与治疗分配无关的其他评估误差，可能引入非差异性测量误差。由于此类误差与治疗分配无系统性关联，通常不会偏袒某一组；相反，它降低精确度并削弱检测真实治疗效应的能力，并且根据结局量表和误差结构，可能减弱观察到的组间差异。
其次，一个相关但不同的现象是照护者安慰剂效应，或称“代理安慰剂效应”，即畜主的期望、治疗偏好或情感投入影响对动物应答的感知和报告，并可能改变照护行为（42）。照护者安慰剂效应已在畜主和兽医中得到记录，包括在随机、双盲、安慰剂对照条件下（43）。期望效应可能增加各治疗组（包括安慰剂接受者）的表观改善，从而降低检测灵敏度；当组间相当，它们不会系统性偏袒任何一组。然而，如果组间期望或感知的治疗分配不同，它们可能引入系统性观察者偏倚并扭曲估计的治疗效应。
最后，畜主相关因素可能影响入组。由于畜主决定其动物是否参与，畜主的动机、治疗偏好、可用资源、日程灵活性和遵守研究程序的意愿可能塑造入组人群。仅通过转诊皮肤科诊所招募可能过度代表患有更严重或难治性AD的犬，而要求频繁就诊、大量诊断检测或排除性饮食的方案可能优先入组拥有更多资源或治疗动机的畜主。这种畜主介导的参与效应可能限制研究人群的代表性和普遍性，即使随机化充分平衡了入组治疗组。
这些偏倚和变异性来源在犬特应性皮炎试验中尤为关键，因为样本量有限、依赖主人报告的结果、疾病异质性以及临床护理的变异性。潜在的缓解措施包括：设盲；经过验证的、互补的主人和研究者评估结果；标准化的评估者培训和研究者-主人沟通；在与研究者会诊前完成主人评估；同步电子日记；在可行的情况下在整个研究期间使用同一主人报告者；依从性监测；以及前瞻性记录伴随治疗、救援治疗和退出原因。
混杂因素和效应修饰因素都是可以影响研究结果的变量，但它们的作用方式不同。混杂因素是与暴露（例如犬特应性皮炎的干预治疗）和结局（例如CADESI）都相关的变量，可能扭曲观察到的两者之间的关系。例如，在一项评估犬特应性皮炎新药的研究中，如果患有跳蚤感染的犬更可能表现出特应性皮炎症状，同时也更可能接受干预，那么跳蚤杀虫剂的使用可能作为混杂因素起作用。如果未适当控制，这可能导致治疗与临床结局之间的虚假关联。
相比之下，效应修饰因素在其各水平上改变治疗与结局之间关联的强度或方向。效应修饰反映的是治疗反应的真实异质性，而非引入偏倚。在同一示例中，如果药代动力学或代谢的差异影响不同品种的药物反应，品种可能作为效应修饰因素起作用(44)。更广泛地说，异质性特应性皮炎综合征中临床或免疫学定义的亚型可能作为效应修饰因素起作用，如果治疗反应在各亚组之间存在差异。某一特定表型区分是否应影响病例定义、分层或预设亚组分析，取决于干预措施和试验目的。
与犬特应性皮炎终点相关的环境暴露
食物过敏原
食物过敏原是犬皮肤病的常见原因，可加重特应性皮炎；它们可能触发具有临床特征且与特应性皮炎无法区分的瘙痒性皮肤病的发作(45–47)。因此，纳入未确诊或未控制食物过敏的犬可能损害旨在评估特应性皮炎干预措施的试验的精确性和准确性。为在解释性疗效试验中尽量减少潜在的食物过敏影响，入选通常要求研究者确定的诊断评估足以排除食物过敏，并在犬的临床病史和既往诊断检查支持时进行消除饮食试验（补充表1）。一旦入选，所有犬应在研究期间保持一致的饮食，以防止饮食诱导的发作扭曲真实治疗效果。
环境过敏原
众多环境过敏原，包括禾草、树木和杂草的花粉，以及昆虫、霉菌、螨虫和微生物过敏原，参与犬特应性皮炎的发病机制(47, 48)。完全避免不可行；暴露因地理和季节而异，可能诱发疾病发作。由于组间环境过敏原暴露的不平衡可能掩盖真实治疗效果(49)，精心设计的临床试验旨在尽可能减少和考虑暴露相关的异质性。这可能包括按季节或地理限制入选、标准化背景护理（例如跳蚤控制），以及按中心或基线疾病严重程度进行区组或分层随机化。在较小规模的研究中，额外的设计和分析策略（例如限制中心数量并预先指定对中心、季节或暴露替代指标的协变量调整）可能有助于减少残余变异性，同时认识到完全控制环境暴露不可实现。
季节性特应性皮炎
季节性变化可影响犬特应性皮炎疾病严重程度的评估(24, 50, 51)。因此，季节性可能影响观察到的治疗效应的幅度或方向（例如，在低过敏原冬季月份入选的犬可能与花粉高峰季节入选的犬反应不同），特别是如果比较组之间的入选在季节上不平衡。在持续时间较长的研究中（例如>90天），潜在的季节性变异可能进一步使治疗反应随时间的解释复杂化。
为减轻这些影响，许多干预性随机对照试验将入选限制为非季节性特应性皮炎的犬，定义为全年有临床症状的犬，同时认识到这些犬仍可能经历季节性加重。因此，即使在非季节性特应性皮炎人群中，也需要仔细考虑入选时机、研究持续时间和随机化，以尽量减少季节性不平衡及其对结局指标的潜在影响。
考虑瘙痒的发作因素
体外寄生虫
在犬中，跳蚤感染（FI）、跳蚤叮咬超敏反应（FBH）以及诸如疥螨病等其他外寄生虫病可引起瘙痒，从而加重或模仿AD的临床体征。为控制这些混杂因素，入组应限于无提示FI、FBH或其他活动性外寄生虫病临床体征的犬（52）。如下文详述，外寄生虫控制方案应在整个RCT期间维持。
细菌/真菌感染
患有犬AD的犬常同时存在细菌和/或真菌（酵母菌）感染（53, 54）。作为研究入组标准，有必要仔细考虑基线时的感染状态（即过度增殖与活动性感染、严重程度和分布），因为皮肤感染可促进瘙痒并诱导或加重炎症，从而使AD的临床体征恶化。为尽量减少感染对犬特应性皮炎结局指标可能产生的影响，患有活动性细菌性毛囊炎或马拉色菌性皮炎的犬通常在研究入组时被排除在AD干预性试验之外（19, 34, 55）。这种方法减少了感染相关瘙痒和炎症所致的混杂，从而能够更清晰地解释归因于研究性治疗的治疗效果。
目前尚无经过验证、普遍接受的单一量化阈值能够区分患有cAD的犬中临床活动性细菌性或马拉色菌性皮炎或耳炎与微生物过度增殖或定植（56）。因此，试验方案应预先规定适合研究目标的操作性定义和标准化评估程序，而非依赖未明确规定的“活动性感染” designation。在实践中，评估可结合相容的临床体征、病变形态和分布、耳镜检查结果以及从预先规定的皮肤部位（以及在相关情况下，耳部部位）获得的细胞学检查，并在有临床指征时进行细菌培养和抗菌药物敏感性试验。由于尚无普遍接受的单一量化阈值或诊断算法，方案应明确规定用于确定感染状态的标准、采样部位和时机、细胞学方法和判定规则、研究者培训以及随机化前感染消退或稳定的标准。在解释性疗效试验中，可在随机化前对临床活动性感染进行治疗并使其稳定，以减少瘙痒和病变终点的混杂。在入组易感染或其他复杂犬AD人群的试验中，可改为将复发性感染的易感性保留为临床表型的一部分，并按下文所述进行前瞻性特征描述（见“多模式治疗和补充终点指标”）。
合并治疗对犬AD症状的影响
抗菌和抗真菌治疗
在患有AD并同时存在皮肤感染的犬中，抗菌和抗真菌治疗可导致临床体征部分或显著减轻（53）。因此，允许合并使用抗菌药物及其时机可对AD结局指标产生实质性影响。为尽量减少感染相关瘙痒和炎症所致的混杂，许多干预性试验在入组时排除患有活动性感染的犬，并要求在基线评估前进行适当的洗脱期（下文讨论）。
或者，一些研究允许合并使用抗菌药物，以更好地反映真实世界的临床实践。在此类设计中，应记录这些治疗的使用、时机和持续时间，并可将其作为次要终点或补救治疗终点报告。疗效的解释应考虑研究旨在分离AD特异性治疗效果，还是在多模式、实用性临床背景下评估治疗表现。
外寄生虫控制
为尽量减少外寄生虫相关病情发作的风险，包括与FI、FBH以及瘙痒性蜱和螨感染（如疥螨病）相关的发作，应在整个研究期间维持有效的外寄生虫控制方案。所用具体产品可能因地理位置和当地寄生虫负荷而异；然而，方案应规定最低覆盖范围和使用要求，并且无论研究中心如何，所有入组犬在整个研究期间的控制应保持一致且不中断。在相关情况下，使用同时具有杀螨活性的药物可进一步降低螨相关瘙痒性发作的风险。同样，旨在减少暴露于AD环境触发因素或其有害后遗症的干预措施可预防或减轻疾病。
洗脱期
洗脱期定义为在基线评估之前停用先前治疗并将其从患者系统中清除的间隔时间。其目的是尽量减少可能混杂治疗反应解释的遗留效应。所需持续时间因药物而异；一般而言，与局部用药相比，全身治疗需要更长的洗脱期，而缓释制剂与非缓释制剂相比也需要更长的洗脱期。
已发表的犬特应性皮炎方案说明了洗脱要求如何根据治疗类别、制剂和给药途径而变化。例如，在ilunocitinib注册试验中，lokivetmab需要八周洗脱期(22)。潜在的残留顾虑在临床上具有合理性，因为lokivetmab可在给药后产生持续数周的止痒效果(57, 58)；然而，现有数据并未将8周确立为普遍验证的洗脱阈值。糖皮质激素方案同样区分了长效注射制剂（如醋酸甲泼尼龙），需要六至八周洗脱期，以及短效制剂（如琥珀酸甲泼尼龙），需要约4周。在FDA犬特应性皮炎注册试验中，洗脱期从口服抗菌和抗真菌药物的1周至长效注射抗菌药物的4周不等(21, 34)。某些局部治疗被分配长达14天的洗脱期。更广泛地说，这些间隔应被视为方案先例而非普遍验证的阈值。洗脱选择应考虑治疗的制剂和给药途径、任何潜在感染的消退以及对所选临床结局指标的潜在残留效应。药代动力学消除、靶点结合和药效学持续时间以及可测量临床获益的持续时间是相关但不同的考虑因素。当缺乏药物特异性证据时，消除半衰期可提供初步参考，但不应单独使用(59)，而皮内过敏试验推荐的停药间隔可提供额外的实用指导(60)。
在犬特应性皮炎试验中纳入洗脱期并非易事。虽然较长的洗脱期可降低残留效应的风险，但也可能因疾病未治疗而加重临床症状。对于起效延迟或生物效应延长的全身性治疗，这一挑战更为复杂，固定时间洗脱可能无法完全反映残留活性。因此，延长的洗脱要求可能引入伦理和实践限制，特别是在病情较重的犬中，会限制招募并降低主人入组的意愿。
根据试验目标，替代设计可减少对统一、冗长洗脱期的依赖，这些洗脱期可能难以实施。替代选项包括采用标准化稳定背景治疗进行的试验；添加、保类固醇或保抗菌药设计（见“多模式治疗和补充终点指标”）；活性对照试验，即研究干预与已批准疗法而非安慰剂进行比较；以及随机撤药设计。还可纳入预先指定的救援治疗算法，并在治疗效果的定义和分析中前瞻性地处理救援使用（见“多模式治疗和补充终点指标”）。
一线犬特应性皮炎治疗方案的研究设计惯例
案例研究
关键的oclacitinib（Apoquel®，Zoetis）注册试验说明了评估一线犬特应性皮炎治疗的关键研究设计方法(34)。随后的ilunocitinib（Zenrelia™，Elanco）注册试验在很大程度上保留了oclacitinib试验中建立的设计框架：多中心、随机、双盲、安慰剂对照设计，主要疗效在第28天评估(22)。尽管方案在某些操作特征上有所不同，但两者应用了相同的核心方法学原则，包括定义的诊断和入选标准、药物特异性洗脱期、伴随治疗限制、随机治疗分配和盲法。因此，我们详细检查oclacitinib方案，以展示如何使用这些设计要素来减轻潜在偏倚来源并最小化终点评估中的误差。
病例定义
为最大化内部有效性，oclacitinib注册研究应用Prélaud标准作为犬特应性皮炎的预先指定临床病例定义，该诊断框架早于前瞻性衍生的Favrot标准(34, 54, 61)。无论使用何种具体临床标准，一致应用预先指定的病例定义可促进标准化入组并支持内部有效性；然而，所选框架的组成标准和诊断性能差异可能影响病例分类、入组人群的构成以及研究结果的普遍性。
为进一步减少与AD表型相关的环境暴露和发作诱因的影响，研究者排除了食物过敏、FBH、细菌性或马拉色菌性皮炎和/或耳炎、体内外寄生虫感染、代谢性疾病及其他疾病的犬只。严格筛选病例入组可最大限度减少来自外来发作诱因的统计噪声，从而增强治疗与结局之间的因果关联。然而，通过招募同质性AD病例亚群来提高内部效度的代价是外部效度的降低。研究结果可推广至具有可比临床特征的犬只，但对其他AD表型或更复杂的临床表现可能适用性较差。在旨在纳入更广泛或更复杂人群的试验中，并发细菌性或马拉色菌性皮炎或耳炎无需绝对排除，但应根据适合试验目标的预设标准进行评估和管理（见“细菌/真菌感染”）。
遗留效应
为确保CADESI-02和PVAS的改善归因于奥拉替尼而非既往药物的残留效应，方案设定了针对具体药物的洗脱间隔。洗脱时长与各药物的药效动力学相匹配：长效糖皮质激素为6周；口服糖皮质激素、环孢素、长效注射用抗菌药及其他具有已知止痒活性的杂类化合物（包括Staphage Lysate（SPL；Delmont Laboratories Inc.，Swarthmore，PA，United States）、加巴喷丁、单胺氧化酶抑制剂和他克莫司）为4周；外用NSAIDs或外用类固醇为3周；抗组胺药为2周；全身性抗菌或抗真菌药为1周。这些洗脱措施最大限度减少了遗留偏倚，确保临床反应完全归因于研究治疗而非既往干预的残留效应。然而在实践中，长时间洗脱可能不切实际甚至不符合伦理。对于瘙痒严重的犬只，主人可能不愿停止缓解症状的治疗；而随着诊疗标准的演变和合格患犬池的缩小，研究者可能难以招募到动物。
合并治疗
为尽量减少合并治疗对CADESI-02和PVAS结局测量的混杂影响，方案提供两种选择：停用该治疗并设置相应洗脱期，或在预设的最低使用/最低频率规则下继续使用[见Cosgrove等，补充表1（34）]。重要的是，在第28天主要终点评估完成之前，禁止使用药用香波和所有全身性或外用抗微生物药（即具有止痒活性的干预措施）。
因无关慢性疾病（如甲状腺功能减退、骨关节炎）接受治疗的犬只，仅在治疗方案于第0天前至少6周未改变且预计在28天研究期间不会改变的情况下方可入组。该要求进一步降低了合并用药变化对基于病变或瘙痒的终点产生偏倚的风险。
设盲与随机化
最后，该试验设计为前瞻性、随机、双盲、安慰剂对照研究。设盲使主人、研究者和数据评估者均不知晓治疗分配。设盲有助于最大限度减少治疗预期的影响，当研究者评估的CADESI和主人评估的PVAS等结局具有主观性时，这一点尤为重要（62）。
随机化完全凭偶然将犬只分配至治疗组或安慰剂组；在样本量充足的情况下，该过程可平衡各组间已知和未知的预后因素，最大限度减少选择偏倚并支持有效的统计推断。随机化和设盲共同增强了研究的内部效度，并增强了对以下结论的信心：结局的任何差异反映的是奥拉替尼的效应，而非随机误差或系统误差所致的虚假关联。
临床试验设计及犬特应性皮炎异质性的考量
设计良好的犬AD试验，以奥拉替尼和伊鲁诺替尼注册研究为例，纳入了若干核心研究设计要素（表2）。方案应：（i）事先指定经过验证的终点指标（如CADESI和PVAS）；（ii）采用严格的入选标准以确保研究人群具有真正的AD诊断；（iii）考虑可能直接影响犬AD的参数（如强制进行跳蚤治疗以控制FI和FBH）。然而，尽管这些核心原则至关重要，标准化的“一刀切”方法仍不够充分，因为它可能无法应对不同患者人群和治疗目标之间具有临床意义的差异。
Table 2. Suggested design considerations for randomized clinical trials in canine atopic dermatitis.
| Trial-design component | Recommendation |
|---|---|
| Case definition and eligibility | Apply a validated, prespecified case definition (e.g., Favrot criteria). Exclude relevant differential diagnoses and prespecify how food-induced AD and potentially confounding comorbidities, including flea bite hypersensitivity, ectoparasite infestation, and bacterial or Malassezia infection, will be excluded, treated, stabilized, or otherwise accounted for at study entry. |
| Ectoparasite control | Exclude active ectoparasite infestation at study entry and maintain a consistent, protocol-defined ectoparasite-control regimen throughout the trial. If products vary among sites, prespecify minimum coverage and dosing requirements. |
| Washout period | Prespecify medication-specific washout periods based on formulation, route of administration, pharmacokinetic and pharmacodynamic properties, and potential residual effects on clinical outcomes. For antimicrobial therapies, also consider whether the treated infection has clinically resolved before baseline. Regard published intervals as protocol precedents rather than universally validated thresholds. |
| Concomitant medications | Prespecify which therapies are prohibited, permitted, or standardized. Record and report their use, timing, and duration, and consider rescue-treatment use as a supportive outcome. |
| Randomization and blinding | Use an adequately powered sample and an appropriate randomization scheme; consider blocked or stratified allocation in smaller trials. Maintain masking of owners, investigators, and outcome assessors whenever feasible. |
| Endpoint selection | Consistent with COSCAD recommendations, include both owner-assessed pruritus (PVAS) and veterinarian-assessed skin-lesion severity (CADESI). Within this framework, select the primary endpoint based on the intervention’s intended effect and mechanism (e.g., PVAS for a pruritus-targeted agent), and retain complementary COSCAD measures as secondary or supportive endpoints to characterize effects across other clinically relevant disease domains. |
| Assessment timing | Consistent with the clinical goal of rapid symptom control, Day 14 or Day 28 may be appropriate primary efficacy time points for trials of frontline treatments in uncomplicated mild-to-moderate AD. For moderate-to-severe, refractory, or otherwise complex AD, a later primary or key efficacy assessment beyond Day 28 may be warranted to account for greater disease complexity and capture delayed or evolving treatment responses. |
| Owner–investigator and proxy-reporting effects | Use validated, complementary owner- and investigator-assessed instruments. Standardize instructions and assessor training, obtain owner assessments before investigator consultation, use contemporaneous diaries, and retain the same owner-reporter whenever feasible. |
鉴于犬AD的多因素性和免疫学复杂性，试验方法学必须具有适应性，以考虑疾病异质性和所研究干预措施的具体作用机制。在设计方案时，应仔细考虑以下因素：犬的治疗史（即从未接受过AD治疗的无治疗史犬与对既往治疗反应极小或无反应的难治性犬）、疾病严重程度（即轻至中度与中至重度）、治疗目标的时机（即即时症状缓解与持续疗效和缓解维持），以及干预的具体靶点（即止痒与减轻皮肤炎症与恢复皮肤屏障功能）。未能考虑这些因素可能导致误导性结论，并可能面临对所研究治疗干预措施错误定性的风险。
为说明疾病严重程度和治疗史如何影响试验设计，我们重点阐述一线治疗的方法学与难治性病例二线治疗的方法学有何不同。
疾病严重程度、治疗方式以及主要终点测量的时间点
评估研究终点所需的时间受疾病严重程度影响，而疾病严重程度决定了治疗目标和预期。在轻至中度犬AD的注册研究中，随机对照试验通常优先考虑快速缓解症状，并在较早的时间点评估终点（图2）。相比之下，在旨在评估重度或难治性病例治疗反应的研究中，重点转向长期疾病管理，这些犬可能对标准治疗无反应、可能需要多模式治疗方法，和/或经历复发。在针对更复杂、重度AD病例（通常表现为复发性微生物皮肤感染）设计的研究中，仅在第28天进行主要终点评估可能不足以区分与抗菌产品相关的症状改善和归因于研究干预的改善。我们建议研究者在这些人群中考虑将主要或关键评估窗口延长至第28天之后（例如延长至第56天或第84天，如图2所示）。这些时间点仅为示例而非规定性的；主要终点的时间安排应基于干预效果的预期起效时间和持续时间、研究人群以及伴随治疗的管理。
[图：犬特应性皮炎（AD）临床试验的示例性研究设计示意图。犬在第0天随机分组，并接受]
研究终点的评估时间点还应与干预的预期临床获益相一致，以及相应的研究目标是证明即刻症状缓解还是更复杂病例的长期管理（图2）。例如，环孢素等通常需要4-6周才能显示临床效果的干预措施（9），可能需要更长的研究持续时间。相反，对于皮质类固醇或JAK抑制剂等能快速缓解瘙痒和炎症的治疗，较短的评估期可能更为合适。
治疗方式与终点选择
在确定犬AD临床试验的主要终点时，必须使这些指标与所评估干预的治疗目标相一致。例如，专门靶向瘙痒受体或神经通路的新兴疗法的出现，有望解决与犬AD相关的严重瘙痒。最近的转化研究表明，靶向IL-31抑制的药物能有效减轻瘙痒，同时对局部皮肤炎症的影响极小（57, 63）。因此，对于靶向瘙痒的药物，指定瘙痒终点（如PVAS）而非皮肤病变终点（如CADESI）作为主要结局可能是有必要的，从而允许使用与干预机制和预期用途最密切相关的结局来评估疗效。重要的是，其他推荐的COSCAD结局指标，特别是兽医评估的皮肤病变严重程度（如CADESI），通常应保留为次要或支持性终点，以描述AD其他临床相关领域的效应，并避免将瘙痒的改善解释为更广泛的疾病控制。
多模式治疗与补充终点指标
在需要多模式治疗方法的临床情境中，应考虑补充已建立终点（如CADESI和PVAS）的指标。例如，研究表明，在开始环孢素或奥拉替尼治疗时，短期同时给予糖皮质激素是有益的（35, 64）。在一项环孢素研究中，糖皮质激素的联合给药加速了瘙痒和CADESI评分的降低。在另一项奥拉替尼研究中，同时给予糖皮质激素治疗降低了反跳性瘙痒的可能性。治疗节省效应（如“激素节省”）和强调安全性参数应成为此类多模式治疗方法的关键指标。同样，在纳入可能出现并发皮肤感染的犬的研究中，也应考虑将反映抗生素或抗菌剂药物节省效应的指标作为治疗成功的指标。
救援药物的使用和随机化治疗的终止是随机化后事件，可能影响后续结局的解释（65, 66）。研究方案和统计分析计划应前瞻性地规定如何定义、记录这些事件，并将其纳入所关注的疗效和相应分析中。在犬AD试验中，退出研究随访可能特别具有信息价值，因为主人可能会撤回临床体征仍未得到充分控制的犬，以避免延长其不适。奥拉替尼注册试验中观察到的差异性退出说明了潜在后果（表1， attrition bias示例）；此类退出可能使疗效估计产生偏倚，应通过前瞻性定义的救援标准、在可行时继续收集结局数据以及针对信息性脱落进行敏感性分析来预先应对。
在解释性疗效试验中，可在随机分组前对具有临床活动性的继发感染进行治疗并使其稳定，以减少对瘙痒和皮肤病变终点的混杂影响。相比之下，纳入易感染或其他复杂犬AD群体的试验可能将反复感染的易感性保留为临床表型的一部分，而非将其排除。在这些试验中，应记录反复感染和抗菌药物使用的基线病史，并可酌情将其作为分层因素或潜在效应修饰因子纳入。偶发感染、抗菌药物暴露和补救治疗的使用应作为结局或影响疗效解释的随机化后事件进行前瞻性采集，与上述补救用药的处理方式一致。在允许使用抗菌或抗菌消毒治疗的情况下，方案应预先规定治疗算法，包括药物选择、给药途径、剂量和疗程；缓解或稳定的标准及其相对于终点评估的时间；以及记录治疗暴露和依从性的程序。
理论上的研究设计、不断演变的标准治疗以及现实世界的可行性
在设计犬AD临床试验时，必须考虑现实世界的实际问题，因为理想的理论方法在日常临床环境中并不总是可行。虽然某些方法学或方案在纸面上可能看起来最佳，但诸如识别和招募受试者的能力、客户依从性、伦理考量、资源可用性以及预算和后勤限制等因素往往决定研究的成败。
历史试验设计可以提供有价值的先例；然而，研究设计必须适应不断演变的标准治疗和结局测量的进步。例如，在COSCAD'18核心结局集发表后，0–10口头数字量表被验证用于评估犬的瘙痒(30)。特定工具的选择应继续以当前专家共识、相关工具验证文献和个体试验的目标为依据。因此，不应假定旨在测量同一结局领域（如瘙痒）的不同工具可以互换使用。奥拉替尼和伊卢诺替尼注册试验对比鲜明的招募经验说明了不断演变的临床格局的潜在影响。尽管这些试验在某些操作特征上有所不同（补充表1），但它们采用了相似的安慰剂对照设计框架，使用了大致可比的入组标准来招募患有犬AD的犬，并涉及相似数量的参与诊所。尽管存在这些相似之处，奥拉替尼研究在不到6个月内完成，从2009年8月至11月，而伊卢诺替尼研究耗时超过3年，从2020年5月至2023年6月(13, 67)。这种差异表明，有效的犬AD治疗日益可及可能在现实世界条件下造成了及时招募的实际和伦理障碍，尤其是对于安慰剂对照试验。
随着治疗选择的进步，研究方案需要现代化，以确保参与者不被剥夺有效治疗，也不被暴露于已知劣于或不及现有替代方案的干预措施。这种方法使研究能够满足不断变化的客户期望并避免伦理困境。个体试验的报告同样应跟上当前标准，例如专门为客户拥有和收容所拥有的犬猫试验制定的PetSORT共识声明中概述的标准，以便透明地描述设计决策(68, 69)。
结论
犬AD是一种异质性综合征，呈现多方面的临床挑战(3–6)，需要涵盖局部和全身治疗的定制化治疗方法(7, 8)。犬常用的全身性止痒和抗炎药物种类同样多样，包括JAK抑制剂、lokivetmab、环孢素和糖皮质激素；这些药物在作用方式、起效时间和不良反应发生率方面各不相同(8, 9)。2023年美国动物医院协会指南强调“治疗过敏犬并非一刀切”，凸显了需要个体化治疗策略，考虑继发感染、急性炎症发作、患者变异性和客户依从性及经济因素等因素(9)。推而广之，在犬AD中开展RCT也没有一刀切的方法学。
采用统一的试验方法可能会忽视疾病表现、严重程度和治疗反应方面具有临床意义的差异。标准终点也可能无法充分反映疾病对犬特应性皮炎患者及其主人造成的更广泛负担，尤其是在伴有反复皮肤感染等合并症的亚组中。因此，取得进展需要灵活的研究设计，使入选标准、洗脱规则和结局指标与所研究的表型相匹配，并辅以适应性方案和以患者为中心的终点，从而更好地反映真实世界的异质性。通过这些方法，结合持续开展的转化研究，兽医界可以加速开发有效疗法，以满足犬特应性皮炎患者群体的多样化需求。
查看英文原文▾
Canine atopic dermatitis (AD) is a chronic inflammatory and pruritic skin disease affecting up to 15% of dogs, with clinical expression shaped by genetic, environmental, and microbial factors. Although the International Committee for Allergic Diseases of Animals (ICADA) established COSCAD as a core outcome set providing standardized outcome measures for evaluating treatment efficacy, comparatively little attention has been given to the upstream methodological considerations that determine the validity and interpretability of trial results. This narrative review uses a structured methodological framework to examine key sources of random error, bias, confounding, and effect modification that can compromise randomized controlled trials (RCTs) in canine AD. We identify critical parameters requiring careful control in trial design, including food and environmental allergen exposures, seasonality, flea infestation, concurrent bacterial and fungal infections, concomitant therapies, and washout period determination. Historical study protocols, conducted primarily in treatment-naïve dogs with mild-to-moderate disease, are analyzed to illustrate how pivotal registration trials mitigated these sources of error through strict case definitions, medication-specific washout intervals, concomitant therapy restrictions, and rigorous blinding and randomization. We further examine the trade-offs between internal validity and external generalizability, and the growing tension between traditional explanatory trial designs and real-world feasibility in an evolving therapeutic landscape. Synthesizing perspectives from a panel of veterinary dermatology experts, we highlight how disease severity, treatment history, and therapeutic modality should inform eligibility criteria, endpoint selection, and assessment timing. Based on these assessments, we highlight the limitations of applying standardized study design methodologies to such a heterogeneous disease. Applying uniform methodologies to such a heterogeneous syndrome risks obscuring clinically meaningful differences in disease presentation and treatment response. Progress requires flexible, fit-for-purpose study designs that align key methodological elements with the phenotype under investigation, enabling accurate interpretation of treatment effects and more effective therapeutic development.
Introduction
Canine atopic dermatitis (AD) is a chronic inflammatory and pruritic skin disease that affects up to 15% of all dogs, making it one of the most prevalent and commonly treated conditions in veterinary clinics (1, 2). The clinical manifestation of canine AD encompasses a wide spectrum of presentations, reflecting the complex interplay of various contributing factors (3); clinical expression is shaped by genetic predisposition (e.g., breed-associated phenotypes), lesion distribution (localized versus generalized), stage of the disease (acute flaring versus chronic), epidermal-barrier defects, and the presence of cutaneous dysbiosis leading to microbial infections or other flare factors (4–6). Because of this complexity, many dogs require a multimodal treatment approach that includes topical and systemic therapies to provide itch relief and to resolve lesions associated with cutaneous inflammation (7–9).
Four systemic drug classes are currently approved by the FDA for treatment of canine AD. The calcineurin inhibitor ciclosporin (Atopica, Elanco) was the first immunomodulator approved for the treatment of canine AD in 2003, with a ciclosporin oral solutions subsequently approved in 2020 (Cyclavance, Virbac) and 2023 (Modulis, CEVA) (10, 11). More recently, oclacitinib (Apoquel, Zoetis), the first Janus-kinase (JAK) inhibitor for veterinary use, was introduced in 2014 (12). A second JAK inhibitor, ilunocitinib (Zenrelia, Elanco), gained approval in 2024 (13). Most recently, the Committee for Veterinary Medicinal Products (CVMP) adopted a positive opinion for a third highly selective JAK1 inhibitor, atinvicitinib (Numelvi, Merck) in 2025 (14). The first monoclonal antibody (mAb) approved for a canine disease by the United States Department of Agriculture (USDA), the anti-interleukin (IL)-31 lokivetmab (Cytopoint, Zoetis) (15, 16), became available in 2017.
Despite these advances, an estimated 10 to 30% of dogs fail to respond, relapse, and/or experience side effects that necessitate discontinuation of conventional treatments (8, 17–19). The multifactorial nature of AD, characterized by a diverse array of genetic, immunologic, and environmental contributors requires a nuanced and personalized approach to the study of novel treatments and patient subgroups. Consequently, to advance the development of canine AD treatment options and optimize patient care, study designs that capture the heterogeneity of this complex and multifactorial condition are needed.
Clinical practice guidelines and narrative reviews have comprehensively summarized therapeutic options for canine AD and the underlying clinical evidence (7–9, 20). Accordingly, this review does not aim to reiterate treatment recommendations or to provide a systematic review or meta-analysis, but rather to examine how study design choices influence the conduct and interpretation of randomized clinical trials (RCTs) in canine AD. We begin by reviewing the primary endpoints established for canine AD and consider how random and systematic errors can distort observed associations, leading to overestimation, underestimation, or reversal of the true treatment effect. We then analyze historical RCT protocols, conducted primarily in treatment-naïve dogs with mild-to-moderate disease, to illustrate how earlier studies were designed to mitigate these sources of error.
Studies were selected from the peer-reviewed literature, with primary emphasis on published pivotal registration trials supporting regulatory authorization by the FDA, USDA, and/or EMA of contemporary systemic therapies for canine AD, including oclacitinib, lokivetmab, and ilunocitinib (Supplementary Table 1) (15, 16, 19, 21–24). These trials were selected because they provide established regulatory precedents for canine AD trial design. The relevant trials were identified using publicly available Freedom of Information summaries and associated regulatory documentation, and the corresponding peer-reviewed publications were located through targeted PubMed searches. Additional peer-reviewed publications from 2006 through 2025 were identified through supplementary PubMed searches and evaluated for evidence that supported, qualified, or challenged the interpretations and recommendations presented in this review. Because this was a focused narrative rather than a systematic review, the searches were not intended to be exhaustive or to support formal grading of evidence certainty.
Finally, perspectives from seven experts in veterinary dermatology and clinical trial design (see Acknowledgements) were obtained to contextualize methodological trade-offs across disease severities and treatment settings. The experts were selected by the authors based on their published expertise and/or clinical trial experience in canine AD. Input was elicited during a virtual roundtable using a structured discussion guide addressing methodological topics identified by the authors in advance. The authors documented and synthesized the feedback and used it to inform the relevant sections of the manuscript. These perspectives informed the discussion of how study-design approaches may require adaptation to disease severity, treatment setting, and anticipated therapeutic effect. Collectively, they underscore the limitations of a one-size-fits-all approach to trial design in a heterogeneous disease, which may obscure clinically meaningful treatment signals within distinct patient subgroups.
Endpoints established for canine AD studies
The primary goal of RCTs, the gold standard for determining the effect of therapeutic interventions, is to obtain valid and quantifiable measures of the treatment effect on patient outcomes (25). Well-designed RCTs require the measurement of study endpoints that provide reliable signals of the intervention being tested. In dermatologic disorders such as canine AD, assessing efficacy is challenging because objective laboratory markers of disease severity are lacking (26–28). To address this, the International Committee for Allergic Diseases of Animals (ICADA) established a core outcome set (COS) of subjective but validated instruments to grade the severity of skin lesions and pruritus for canine AD (COSCAD) (29, 30).
The Canine Atopic Dermatitis Extent and Severity Index (CADESI) is a composite scoring index that is used by veterinary dermatologists to systematically score the severity of skin lesions in atopic dogs (31, 32). The Pruritus Visual Analog Scale (PVAS), an owner assessed instrument, is used to evaluate the severity of pruritus (30, 33). Accordingly, these instruments are the most common primary endpoints used in canine AD RCTs (19, 24, 34, 35). To enhance the depth and breadth of a study’s findings, investigators can also include standardized secondary endpoints such as owner global assessment of treatment efficacy (OGATE) and investigator global assessment (2D-IGA). Incorporating these additional measures deepens study insights that can support clinical decision-making and guide future research (29).
Randomization, random error, bias, confounding and effect modification in canine AD studies
Although validated endpoints have been established for canine AD, random error (or chance) and systematic errors (or systematic bias) need to be minimized to allow for valid and precise inferences between an intervention and outcome(s) to be made (36). Random error, which may be defined as the natural fluctuations that occur in data due to chance, can influence the precision of virtually any outcome measure. Systematic bias, on the other hand, refers to consistent and reproducible errors introduced into the study design, data collection, analysis, and/or reporting that lead to incorrect estimates of the true effect of the intervention. Systematic errors may strengthen, weaken, or completely reverse the true treatment effect (37, 38).
In RCTs, randomization procedures that assign participants to treatment groups by chance increase the likelihood that groups are comparable at baseline by balancing both measured and unmeasured prognostic factors. When implemented correctly, randomization strengthens causal inference by increasing confidence that observed differences in outcomes are attributable to the intervention rather than to confounding variables.
With increasing sample size, randomization more reliably distributes variables associated with the outcome of interest across treatment groups, thereby reducing the risk of chance imbalances. Larger sample sizes also reduce random error, resulting in more precise effect estimates and narrower confidence intervals. However, while randomization improves the probability of balanced groups, perfect comparability cannot be guaranteed in any single trial, particularly when sample sizes are modest. For example, in a randomized controlled trial comparing the oral antihistamine fexofenadine with the active comparator methylprednisolone, baseline imbalances in pruritus scores were observed between treatment groups comprising 15 dogs each (39). Although fexofenadine is not a contemporary standard therapy for canine AD, the study provides a useful methodological example of the potential for chance baseline imbalance in small veterinary trials. Moreover, the wide ranges of baseline CADESI and pruritus scores reported in this study illustrate how substantial within-group heterogeneity can reduce the precision of treatment-effect estimates in small study populations. To mitigate these risks, investigators should incorporate a priori sample size and power calculations and consider randomization strategies tailored to study size and design (e.g., blocked or stratified randomization in smaller trials).
Given the limitations of randomization, additional methodological safeguards may be necessary to reduce the impact of systematic error. In canine AD studies, several factors can significantly influence outcome measurements (e.g., skin lesion and pruritus severity scores) and must be carefully considered in trial design and conduct. Known factors that can trigger acute flares and/or change the clinical features of canine AD include exposure to food and environmental allergens, seasonality, and concurrent skin infections and flea infestations (Figure 1). If not appropriately controlled or accounted for, these factors can introduce bias or confounding, potentially masking true treatment effects. The potential impact of these key parameters on canine AD outcome measures, and how they have been addressed in prior studies, is summarized below.
[图：Overview of the principal disease- and treatment-related factors that may influence primary outcome measures (CADESI and]
Other sources of bias, well recognized in human clinical research, that may be encountered in veterinary clinical trials include selection bias (systematic differences between animals enrolled in a study and those not enrolled), misclassification bias (systematic differences in how exposures or outcomes are measured across groups), recall bias (systematic errors in the reporting of exposures or events), and attrition bias (systematic differences in withdrawals or exclusions) (Table 1) (40). These categories describe systematic errors that can distort the validity of between-group comparisons.
Table 1. Common sources of bias in canine atopic dermatitis clinical trials.
| Type of bias | Description | Illustrative example in a canine AD trial |
|---|---|---|
| Selection bias | Systematic differences between the characteristics of animals selected for the study and those not selected. | A trial recruiting only from referral dermatology practices may enroll dogs with more severe or treatment-refractory AD compared to the general population of atopic dogs, limiting generalizability of results |
| Misclassification bias | Systematic differences in how exposures, outcomes, or covariates are measured or classified between groups | In an unblinded trial, investigators aware of treatment allocation may systematically score CADESI-04 lesions more favorably in dogs receiving the investigational therapy than in those receiving placebo, leading to differential outcome assessment and inflation of the apparent treatment effect |
| Recall bias | Systematic differences in the accuracy or completeness of recalled information between groups | Owners of dogs experiencing more severe or recent atopic dermatitis flares may recall and report prior dietary exposures or environmental triggers differently than owners of dogs with milder disease, potentially creating spurious associations between reported exposures and disease severity |
| Attrition bias | Systematic differences in withdrawals or exclusions of animals from the study between treatment groups | Dogs experiencing inadequate response or adverse events may be more likely to withdraw from one treatment arm, leading to biased estimates of efficacy if missing data are not handled appropriately. For example, in the oclacitinib registration trial, more than 86% of placebo-treated dogs transitioned from the randomized comparison to an open-label study after Day 28, creating differential attrition that the authors noted biased longer-term between-group comparisons. |
| Performance bias | Systematic differences in care, management, or co-interventions between treatment groups apart from the intervention under study | Especially when blinding is incomplete, dogs in one treatment arm may receive more frequent follow-up visits, adjunctive topical therapies, or additional owner counseling than dogs in the comparator group, potentially exaggerating observed treatment effects |
The triadic relationship among the animal, owner, and investigator introduces distinctive methodological considerations in veterinary clinical trials, affecting enrollment, treatment administration, outcome assessment, and study retention. This structure has close analogs in proxy-reported outcomes in human pediatric and geriatric research (e.g., parents reporting on behalf of young children (41), caregivers reporting on behalf of patients with cognitive impairment). Firstly, canine AD trials commonly use owner-assessed PVAS together with investigator-assessed CADESI. Discordance between these measures is not inherently evidence of bias because they assess complementary manifestations of disease captured in different settings: owners observe pruritic behavior longitudinally in the home, whereas investigators assess inflammatory skin lesions during clinic visits. However, inconsistency within either measure, variation among raters, or other assessment error unrelated to treatment allocation may introduce nondifferential measurement error. Because such error is not systematically related to treatment assignment, it generally does not favor one group over another; rather, it reduces precision and weakens the ability to detect a true treatment effect and, depending on the outcome scale and error structure, may attenuate observed between-group differences.
Second, a related but distinct phenomenon is the caregiver placebo effect, or “placebo by proxy,” in which an owner’s expectations, treatment preferences, or emotional investment influence the perception and reporting of the animal’s response and may also alter caregiving behavior (42). Caregiver placebo effects have been documented in both owners and veterinarians, including under randomized, double-masked, placebo-controlled conditions (43). Expectancy effects may increase apparent improvement across treatment groups, including among placebo recipients, and can thereby reduce assay sensitivity; when comparable between groups, they do not systematically favor either group. If expectations or perceived treatment allocation differ between groups, however, they may introduce systematic observer bias and distort the estimated treatment effect.
Finally, owner-related factors may influence enrollment. Because owners determine whether their animals participate, owner motivation, treatment preferences, available resources, schedule flexibility, and willingness to comply with study procedures may shape the enrolled population. Recruitment exclusively through referral dermatology practices may overrepresent dogs with more severe or treatment-refractory AD, while protocols requiring frequent visits, extensive diagnostic testing, or elimination diets may preferentially enroll owners with greater resources or treatment motivation. This owner-mediated participation effect may limit the representativeness and generalizability of the study population, even when randomization adequately balances the enrolled treatment groups.
These sources of bias and variability are particularly consequential in canine AD trials because of modest sample sizes, reliance on owner-reported outcomes, disease heterogeneity, and variability in clinical care. Potential mitigation measures include masking; validated, complementary owner- and investigator-assessed outcomes; standardized assessor training and investigator–owner communication; completion of owner assessments before consultation with the investigator; contemporaneous electronic diaries; use of the same owner-reporter throughout the study when feasible; adherence monitoring; and prospective documentation of concomitant treatment, rescue therapy, and reasons for withdrawal.
Confounders and effect modifiers are both variables that can influence study outcomes, but they do so in distinct ways. A confounder is a variable associated with both the exposure (e.g., interventional treatment for canine AD) and the outcome (e.g., CADESI), and can distort the observed relationship between them. For example, in a study evaluating a new drug for canine AD, flea insecticidal use could act as a confounder if dogs with flea infestation (FI) are more likely to exhibit AD symptoms and are also more likely to receive the intervention. If not appropriately controlled, this could lead to a spurious association between the treatment and clinical outcomes.
In contrast, an effect modifier alters the strength or direction of the association between treatment and outcome across its levels. Rather than introducing bias, effect modification reflects true heterogeneity in treatment response. In the same example, breed could function as an effect modifier if differences in pharmacokinetics or metabolism influence drug response across breeds (44). More broadly, clinically or immunologically defined phenotypes within the heterogeneous AD syndrome may function as effect modifiers if treatment response varies across subgroups. Whether a given phenotypic distinction should inform case definition, stratification, or prespecified subgroup analysis depends on the intervention and trial objective.
Environmental exposures associated with canine AD endpoints
Food allergens
Food allergens are a common cause of dermatologic disease in dogs and can exacerbate AD; they may trigger a flare of a pruritic skin disease that is clinically characteristic and indistinguishable from AD (45–47). Consequently, enrolling dogs with undiagnosed or uncontrolled food allergy can compromise the precision and accuracy of trials designed to evaluate AD interventions. To minimize potential food allergy effects in explanatory efficacy trials, eligibility often requires an investigator-determined diagnostic evaluation sufficient to rule out food allergy, with elimination-diet testing undertaken when warranted by the dog’s clinical history and prior diagnostic work-up (Supplementary Table 1). Once enrolled, all dogs should remain on a consistent diet for the duration of the study to prevent diet-induced flares from distorting the true treatment effects.
Environmental allergens
Numerous environmental allergens, including pollens from grasses, trees, and weeds, as well as insect, mold, mite, and microbial allergens, contribute to the pathogenesis of canine AD (47, 48). Complete avoidance is not feasible; exposure varies by geography and season and may precipitate disease flares. Because imbalances in environmental allergen exposure across groups can obscure true treatment effects (49), well-designed clinical trials aim to minimize and account for exposure-related heterogeneity where feasible. This may include restricting enrollment by season or geography, standardizing background care (e.g., flea control), and using blocked or stratified randomization by site or baseline disease severity. In smaller studies, additional design and analytic strategies (e.g., limiting the number of sites and prespecifying covariate adjustment for site, season, or exposure proxies) may help reduce residual variability, while recognizing that complete control of environmental exposure is not achievable.
Seasonal atopic dermatitis
Seasonal changes can influence the assessment of disease severity in canine AD (24, 50, 51). As such, seasonality may affect the magnitude or direction of observed treatment effects (e.g., dogs enrolled during low-allergen winter months may respond differently than dogs enrolled during peak pollen seasons), particularly if enrollment is imbalanced across seasons between comparison groups. In longer-duration studies (e.g., >90 days), underlying seasonal variation may further complicate interpretation of treatment response over time.
To mitigate these effects, many interventional randomized controlled trials restrict enrollment to dogs with non-seasonal AD, defined as dogs with year-round clinical signs, while recognizing that such dogs may still experience seasonal exacerbations. Accordingly, even within non-seasonal AD populations, careful consideration of enrollment timing, study duration, and randomization is required to minimize seasonal imbalances and their potential impact on outcome measures.
Accounting for flare factors of itch
Ectoparasites
In dogs, flea infestation (FI), flea bite hypersensitivity (FBH), and other ectoparasitic diseases such as sarcoptic mange may cause pruritus that exacerbates or mimics the clinical signs of AD. To control for these confounders, enrollment should be restricted to dogs with no clinical signs suggestive of FI, FBH, or other active ectoparasitic disease (52). As detailed below, ectoparasite-control regimens should be maintained throughout the entire RCT.
Bacterial/fungal infections
Dogs with canine AD frequently present with concurrent bacterial and/or fungal (yeast) infections (53, 54). Careful consideration of infection status at baseline (i.e., overgrowth versus active infection, severity, and distribution) as a study entry criterion is warranted, because cutaneous infections can promote pruritus and induce or exacerbate inflammation, thereby worsening the clinical signs of AD. To minimize the impact infections may have on canine atopic dermatitis outcome measures, dogs with active bacterial folliculitis or Malassezia dermatitis are often excluded at study entry from interventional AD trials (19, 34, 55). This approach reduces confounding by infection-related pruritus and inflammation, allowing for clearer interpretation of treatment effects attributable to the investigational therapy.
No validated, universally accepted quantitative thresholds alone distinguish clinically active bacterial or Malassezia dermatitis or otitis from microbial overgrowth or colonization in dogs with cAD (56). Accordingly, trial protocols should prespecify operational definitions and standardized assessment procedures appropriate to the study objective rather than rely on an unspecified designation of “active infection.” In practice, assessment may combine compatible clinical signs, lesion morphology and distribution, otoscopic findings, and cytology obtained from prespecified skin and, where relevant, otic sites, with bacterial culture and antimicrobial susceptibility testing performed when clinically indicated. Because no single quantitative threshold or diagnostic algorithm is universally accepted, protocols should specify the criteria used to determine infection status, the sites and timing of sampling, cytologic methods and decision rules, investigator training, and criteria for infection resolution or stabilization before randomization. In explanatory efficacy trials, clinically active infection may be treated and stabilized before randomization to reduce confounding of pruritus and lesion endpoints. In trials enrolling infection-prone or otherwise complex canine AD populations, susceptibility to recurrent infection may instead be retained as part of the clinical phenotype and prospectively characterized as described below (see “Multimodal Treatments and Supplemental Endpoint Measures”).
Impact of concomitant treatments on canine AD symptoms
Antibacterial and antifungal therapies
In dogs with AD and concurrent cutaneous infections, antibacterial and antifungal therapy may lead to partial or marked reductions in clinical signs (53). Accordingly, the allowance and timing of concomitant antimicrobial therapies can substantially influence AD outcome measures. To minimize confounding from infection-related pruritus and inflammation, many interventional trials exclude dogs with active infections at enrollment and require an appropriate washout period (discussed below) prior to baseline assessment.
Alternatively, some studies permit concomitant antimicrobial therapy to better reflect real-world clinical practice. In such designs, the use, timing, and duration of these therapies should be documented and may be reported as a secondary or rescue-treatment endpoint. Interpretation of efficacy should account for whether the study is intended to isolate AD-specific treatment effects or to evaluate treatment performance within a multimodal, pragmatic clinical context.
Ectoparasite control
To minimize the risk of ectoparasite-related flares, including those associated with FI, FBH, and pruritic tick and mite infestations such as sarcoptic mange, an effective ectoparasite-control regimen should be maintained throughout the study period. The specific product used may vary according to geographic location and local parasite burden; however, the protocol should define minimum coverage and administration requirements, and control should remain consistent and uninterrupted for all enrolled dogs throughout the study, regardless of site. Where pertinent, use of agents that also provide acaricidal activity may further reduce the risk of mite-associated pruritic flares. Likewise, interventions aimed at reducing exposure to or harmful sequelae from environmental triggers of AD could prevent or mitigate disease.
Washout period
Washout periods are defined as the interval during which prior treatments are discontinued and cleared from a patient’s system before baseline assessment. Their purpose is to minimize carryover effects that could confound interpretation of treatment response. The required duration varies by medication; in general, longer washouts are needed for systemic therapies compared with topical agents, and for depot versus non-depot formulations.
Published canine AD protocols illustrate how washout requirements may vary according to treatment class, formulation, and route of administration. For example, lokivetmab was subject to an eight-week washout in the ilunocitinib registration trial (22). The underlying carry-over concern is clinically plausible because lokivetmab can produce antipruritic effects lasting several weeks after administration (57, 58); however, the available data do not establish 8 weeks as a universally validated washout threshold. Glucocorticoid protocols have similarly distinguished between long-acting injectable formulations (e.g., methylprednisolone acetate), requiring washouts of six to 8 weeks, and shorter-acting formulations (e.g., methylprednisolone succinate), requiring approximately 4 weeks. In FDA registration trials for canine AD, washout periods ranged from 1 week for oral antibacterial and antifungal agents to 4 weeks for long-acting injectable antimicrobials (21, 34). Certain topical therapies have been assigned washouts of up to 14 days. More broadly, these intervals should be regarded as protocol precedents rather than universally validated thresholds. Washout selection should account for the treatment’s formulation and route of administration, resolution of any underlying infection, and potential residual effects on the selected clinical outcome measures. Pharmacokinetic elimination, target engagement and pharmacodynamic duration, and the duration of measurable clinical benefit are related but distinct considerations. When drug-specific evidence is unavailable, elimination half-life may provide a preliminary reference but should not be used in isolation (59), while recommended medication-withdrawal intervals for intradermal allergy testing may offer additional practical guidance (60).
Incorporating washout periods in canine AD trials is not straightforward. Although longer washouts reduce the risk of carryover effects, they may also exacerbate clinical signs as disease remains untreated. This challenge is compounded for systemic therapies with delayed onset or prolonged biological effects, where fixed time-based washouts may not fully capture residual activity. As a result, extended washout requirements can introduce ethical and practical constraints, particularly in dogs with more severe disease, by limiting recruitment and reducing owner willingness to enroll.
Depending on the trial objective, alternative designs may reduce reliance on uniform, lengthy washout periods that may be impractical to implement. Alternative options include trials conducted with standardized stable background therapy; add-on, steroid-sparing, or antimicrobial-sparing designs (see “Multimodal Treatments and Supplemental Endpoint Measures”); active-comparator trials in which the study intervention is compared with an approved therapy rather than placebo; and randomized-withdrawal designs. Prespecified rescue-treatment algorithms may also be incorporated, with rescue use addressed prospectively in the definition and analysis of the treatment effect (see “Multimodal Treatments and Supplemental Endpoint Measures”).
Study design conventions for frontline canine AD treatment options
Case-study
The pivotal oclacitinib (Apoquel®, Zoetis) registration trial illustrates key study design methodologies for evaluating frontline canine AD treatments (34). The subsequent ilunocitinib (Zenrelia™, Elanco) registration trial largely retained the design framework established in the oclacitinib trial: a multicenter, randomized, double-masked, placebo-controlled design with primary efficacy assessed on Day 28 (22). Although the protocols differed in certain operational features, both applied the same core methodological principles, including defined diagnostic and eligibility criteria, medication-specific washout periods, restrictions on concomitant therapies, random treatment allocation, and masking. We therefore examine the oclacitinib protocol in detail to demonstrate how these design elements were used to mitigate potential sources of bias and minimize error in endpoint assessment.
Case-definition
To maximize internal validity, the oclacitinib registration study applied the Prélaud criteria as a prespecified clinical case definition for canine AD, a diagnostic framework that preceded the prospectively derived Favrot criteria (34, 54, 61). Irrespective of the specific clinical criteria used, consistent application of a prespecified case definition promotes standardized enrollment and supports internal validity; however, differences in the component criteria and diagnostic performance of the selected framework may influence case classification, the composition of the enrolled population, and the generalizability of the findings.
To further minimize the influence of environmental exposures and flare triggers associated with AD phenotypes, investigators excluded dogs with food allergies, FBH, bacterial or Malassezia dermatitis and/or otitis, internal and external parasitism, metabolic disease, and other conditions. The recruitment of tightly screened cases minimized statistical noise from extraneous flare triggers, thus strengthening the causal link between treatment and outcome. However, the trade-off for enhancing internal validity by recruiting a homogeneous subset of AD cases is a reduction in external validity. The findings may be generalized to dogs with comparable clinical profiles but may be less applicable to other AD phenotypes or more complex clinical presentations. In trials intended to enroll broader or more complex populations, concurrent bacterial or Malassezia dermatitis or otitis need not be categorically excluded but should be assessed and managed according to prespecified criteria appropriate to the trial objective (see “Bacterial/Fungal Infections”).
Carry-over effect
To ensure that improvements in CADESI-02 and PVAS were attributable to oclacitinib rather than lingering effects of previous drugs, the protocol imposed medication-specific washout intervals. Wash-out durations were matched to each agent’s pharmacodynamics: 6 weeks for depot glucocorticoids; 4 weeks for oral glucocorticoids, ciclosporin, long-acting injectable antimicrobials, and other miscellaneous compounds with known antipruritic activity, including Staphage Lysate (SPL; Delmont Laboratories Inc., Swarthmore, PA, United States), gabapentin, monoamine oxidase inhibitors, and tacrolimus; 3 weeks for topical NSAIDs or topical steroids; 2 weeks for antihistamines; and 1 week for systemic antibacterial or antifungal agents. These wash-outs minimized carry-over bias, ensuring that clinical responses were attributable solely to the study treatment and not to residual effects from prior interventions. In practice, however, lengthy washouts can be impractical or even unethical. Owners may be reluctant to withhold relief from severely pruritic dogs, while investigators may struggle to recruit animals as the standard of care evolves and the pool of eligible patients shrinks.
Concomitant therapy
To minimize concomitant treatments from confounding CADESI-02 and PVAS outcome measurements, the protocol offered two options: discontinue the treatment with a corresponding washout period or continue their use under predefined minimal-use/minimal-frequency rules [see Cosgrove et al., Supplementary Table 1 (34)]. Importantly, medicated shampoos and all systemic or topical antimicrobials (i.e., interventions with antipruritic activity), were prohibited until after the Day 28 primary endpoint assessment.
Dogs receiving therapy for unrelated chronic disorders (e.g., hypothyroidism, osteoarthritis) could enroll only if the regimen had been unchanged for at least 6 weeks before Day 0 and it was not expected to change during the 28-day study. This requirement further reduced the risk that shifts in concurrent medication would bias lesion- or pruritus-based endpoints.
Blinding and randomization
Finally, the trial was designed as a prospective, randomized, double-blind, placebo-controlled study. Blinding kept owners, investigators, and data assessors unaware of treatment allocation. Blinding helps minimize the influence of treatment expectations, which is particularly important when outcomes such as investigator-assessed CADESI and owner-assessed PVAS are subjective (62).
Randomization assigns dogs to treatment or placebo purely by chance; with adequate sample size, this process balances both known and unknown prognostic factors across groups, minimizing selection bias and supporting valid statistical inference. Together, randomization and blinding enhance the internal validity of the study and bolster confidence that any differences in outcomes reflect the effect of oclacitinib rather than spurious associations secondary to random or systematic errors.
Clinical trial design and accounting for canine atopic dermatitis heterogeneity
Well-designed canine AD trials, exemplified by the oclacitinib and ilunocitinib registration studies, incorporate several core study design elements (Table 2). Protocols should: (i) a priori specify validated endpoint measures (e.g., CADESI and PVAS); (ii) employ rigorous eligibility criteria to ensure the study population has a true AD diagnosis; and (iii) account for parameters that may directly influence canine AD (e.g., mandate flea treatment to control for FI and FBH). However, while these core principles are essential, a standardized, one-size-fits-all approach is insufficient, as it may fail to address the clinically significant variations across different patient populations and treatment goals.
Table 2. Suggested design considerations for randomized clinical trials in canine atopic dermatitis.
| Trial-design component | Recommendation |
|---|---|
| Case definition and eligibility | Apply a validated, prespecified case definition (e.g., Favrot criteria). Exclude relevant differential diagnoses and prespecify how food-induced AD and potentially confounding comorbidities, including flea bite hypersensitivity, ectoparasite infestation, and bacterial or Malassezia infection, will be excluded, treated, stabilized, or otherwise accounted for at study entry. |
| Ectoparasite control | Exclude active ectoparasite infestation at study entry and maintain a consistent, protocol-defined ectoparasite-control regimen throughout the trial. If products vary among sites, prespecify minimum coverage and dosing requirements. |
| Washout period | Prespecify medication-specific washout periods based on formulation, route of administration, pharmacokinetic and pharmacodynamic properties, and potential residual effects on clinical outcomes. For antimicrobial therapies, also consider whether the treated infection has clinically resolved before baseline. Regard published intervals as protocol precedents rather than universally validated thresholds. |
| Concomitant medications | Prespecify which therapies are prohibited, permitted, or standardized. Record and report their use, timing, and duration, and consider rescue-treatment use as a supportive outcome. |
| Randomization and blinding | Use an adequately powered sample and an appropriate randomization scheme; consider blocked or stratified allocation in smaller trials. Maintain masking of owners, investigators, and outcome assessors whenever feasible. |
| Endpoint selection | Consistent with COSCAD recommendations, include both owner-assessed pruritus (PVAS) and veterinarian-assessed skin-lesion severity (CADESI). Within this framework, select the primary endpoint based on the intervention’s intended effect and mechanism (e.g., PVAS for a pruritus-targeted agent), and retain complementary COSCAD measures as secondary or supportive endpoints to characterize effects across other clinically relevant disease domains. |
| Assessment timing | Consistent with the clinical goal of rapid symptom control, Day 14 or Day 28 may be appropriate primary efficacy time points for trials of frontline treatments in uncomplicated mild-to-moderate AD. For moderate-to-severe, refractory, or otherwise complex AD, a later primary or key efficacy assessment beyond Day 28 may be warranted to account for greater disease complexity and capture delayed or evolving treatment responses. |
| Owner–investigator and proxy-reporting effects | Use validated, complementary owner- and investigator-assessed instruments. Standardize instructions and assessor training, obtain owner assessments before investigator consultation, use contemporaneous diaries, and retain the same owner-reporter whenever feasible. |
Given the multifactorial and immunologically complex nature of canine AD, trial methodologies must be adaptable to account for disease heterogeneity and the specific mechanism of action of the intervention under study. In designing a protocol, careful consideration should be given to factors such as a dog’s treatment history (i.e., treatment-naïve dogs with no prior exposure to AD treatment(s) versus refractory dogs with minimal or no therapeutic response to prior treatment), severity of disease (i.e., mild-to-moderate versus moderate-to-severe), timing of treatment goals i.e., immediate symptom relief versus sustained efficacy and remission maintenance, and the specific target of intervention (i.e., itch relief versus reduction of cutaneous inflammation versus restoration of skin barrier function). Failure to account for these factors may result in misleading conclusions and may risk mischaracterizing the therapeutic intervention under study.
To illustrate how disease severity and treatment history influence trial design, we highlight how the methodology for a frontline treatment differs from that for second-line therapies in treatment-refractory cases.
Disease severity, therapeutic modality, and time point of primary endpoint measurement
The time required to assess study endpoints is influenced by disease severity, which shapes treatment goals and expectations. In registration studies of mild-to-moderate canine AD, RCTs often prioritize rapid symptom relief, with endpoints evaluated at earlier timepoints (Figure 2). In contrast, the focus shifts to longer-term disease management in studies designed to evaluate treatment response in severe or refractory cases where dogs may fail to respond to standard treatments, may require a multimodal treatment approach, and/or experience relapses. In studies designed for more complex, severe AD cases which often present with recurrent microbial skin infections, primary endpoint assessment at Day 28 alone may be insufficient to differentiate symptom improvements associated with antimicrobial products from improvements attributed to the intervention under study. We recommend that investigators consider extending the primary or key assessment window beyond Day 28 (e.g., to Day 56 or Day 84, as illustrated in Figure 2) in these populations. These time points are illustrative rather than prescriptive; the timing of the primary endpoint should be informed by the anticipated onset and duration of the intervention’s effect, the study population, and the management of concomitant therapies.
[图：Illustrative study design schema for canine atopic dermatitis (AD) clinical trials. Dogs are randomized on Day 0 with gr]
The time point assessment of the study endpoint(s) should also align with the intended clinical benefit of the intervention and whether the corresponding study goal is to demonstrate immediate symptom relief or long-term management of more complex cases (Figure 2). For example, interventions like ciclosporin, which typically require 4–6 weeks to show clinical effects (9), may necessitate longer study durations. Conversely, shorter assessment periods may be suitable for treatments like corticosteroids or JAK inhibitors, which offer rapid relief of pruritus and inflammation.
Therapeutic modality and endpoint selection
In determining the primary endpoint(s) for clinical trials in canine AD, it is imperative to align these measures with the therapeutic objectives of the intervention being evaluated. For instance, the advent of emerging therapies specifically targeting itch receptors or neural pathways holds promise in addressing the profound pruritus associated with canine AD. Recent translational research suggests that agents targeting IL-31 inhibition effectively mitigate pruritus while exerting minimal impact on local skin inflammation (57, 63). Consequently, designating a pruritus endpoint (e.g., PVAS), rather than a skin-lesion endpoint (e.g., CADESI), as the primary outcome may be warranted for pruritus-targeted agents, allowing efficacy to be assessed using the outcome most closely aligned with the intervention’s mechanism and intended use. Importantly, other recommended COSCAD outcome measures, particularly veterinarian-assessed skin-lesion severity (e.g., CADESI), should generally be retained as secondary or supportive endpoints to characterize effects across other clinically relevant domains of AD and to avoid interpreting improvement in pruritus as broader disease control.
Multimodal treatments and supplemental endpoint measures
In clinical scenarios necessitating multimodal treatment approaches, endpoints that complement established endpoints (e.g., CADESI and PVAS) should be considered. For example, studies have shown that short concomitant glucocorticoid administration is beneficial when initiating treatment with ciclosporin or oclacitinib (35, 64). In a ciclosporin study, coadministration of glucocorticoids accelerated reductions in pruritus and CADESI scores. In a separate oclacitinib study, concomitant glucocorticoid therapy reduced the likelihood of rebound pruritus. Treatment sparing (e.g., “steroid sparing”) benefits and an emphasis on safety parameters should be key measures for such multimodal treatment approaches. Likewise, in studies enrolling dogs that are likely to present with concurrent cutaneous infections, metrics capturing drug-sparing effects of antibiotics or antiseptics should also be considered as indicators of treatment success.
Rescue-medication use and discontinuation of randomized treatment are post-randomization events that can affect the interpretation of subsequent outcomes (65, 66). Protocols and statistical analysis plans should prospectively specify how these events will be defined, recorded, and incorporated into the treatment effect of interest and corresponding analysis. Withdrawal from study follow-up may be particularly informative in canine AD trials because owners may withdraw dogs whose clinical signs remain inadequately controlled to avoid prolonging their discomfort. The potential consequences are illustrated by the differential withdrawal observed in the oclacitinib registration trial (Table 1, attrition bias example); such withdrawal may bias treatment-effect estimates and should be anticipated through prospectively defined rescue criteria, continued outcome collection when feasible, and sensitivity analyses addressing informative dropout.
In explanatory efficacy trials, clinically active secondary infection may be treated and stabilized before randomization to reduce confounding of pruritus and skin-lesion endpoints. By contrast, trials enrolling infection-prone or otherwise complex canine AD populations may retain susceptibility to recurrent infection as part of the clinical phenotype rather than excluding it. In these trials, baseline history of recurrent infection and antimicrobial use should be documented and may, as appropriate, be incorporated as stratification factors or potential effect modifiers. Incident infections, antimicrobial exposure, and rescue-treatment use should be prospectively captured as outcomes or post-randomization events affecting treatment-effect interpretation, consistent with the treatment of rescue medication described above. Where antimicrobial or antiseptic therapy is permitted, protocols should prespecify treatment algorithms, including agent selection, route, dose, and duration; criteria for resolution or stabilization and their timing relative to endpoint assessment; and procedures for documenting treatment exposure and adherence.
Theoretical study design, evolving standard-of-care, and real-world feasibility
In designing canine AD clinical trials, it is essential to consider real-world practicalities, as the ideal theoretical approach may not always be feasible in everyday clinical settings. While certain methodologies or protocols may appear optimal on paper, factors such as the ability to identify and recruit subjects, client compliance, ethical considerations, resource availability, and budget and logistical constraints often shape the success of studies.
Historical trial designs can offer valuable precedents; however, study designs must remain adaptable to evolving standards of care and advances in outcome measurement. For example, following publication of the COSCAD’18 core outcome set, the 0–10 verbal numeric scale was validated for assessing pruritus in dogs (30). Selection of a specific instrument should remain informed by current expert consensus, the relevant instrument-validation literature, and the objectives of the individual trial. Accordingly, different instruments intended to measure the same outcome domain, such as pruritus, should not be assumed to be interchangeable. The contrasting recruitment experiences of the oclacitinib and ilunocitinib registration trials illustrate the potential implications of an evolving clinical landscape. Although these trials differed in certain operational features (Supplementary Table 1), they employed similar placebo-controlled design frameworks, used broadly comparable eligibility criteria to enroll dogs with canine AD, and involved a similar number of participating clinics. Despite these similarities, the oclacitinib study was completed in under 6 months, from August to November 2009, whereas the ilunocitinib study took more than 3 years, from May 2020 to June 2023 (13, 67). This disparity suggests that the expanding availability of effective canine AD treatments may have created practical and ethical barriers to timely recruitment under real-world conditions, particularly for placebo-controlled trials.
As therapeutic options advance, study protocols need to be modernized to ensure participants are not withheld effective treatments or exposed to interventions that are known to be inferior or less effective than available alternatives. This approach allows studies to meet evolving client expectations and avoid ethical dilemmas. Reporting of individual trials should likewise keep pace with current standards, such as those outlined in the PetSORT consensus statement developed specifically for trials in client- and shelter-owned dogs and cats, so that design decisions are described transparently (68, 69).
Conclusion
Canine AD is a heterogeneous syndrome that presents a multifaceted clinical challenge (3–6), and requires a tailored approach to treatment that encompasses both topical and systemic therapies (7, 8). The array of systemic antipruritic and anti-inflammatory medications commonly employed in dogs, including JAK inhibitors, lokivetmab, ciclosporin, and glucocorticoids, is equally diverse; these agents vary in their mode of action, time-to-onset, and rates of adverse reactions (8, 9). Underscoring the need for individualized treatment strategies that account for factors such as secondary infections, acute inflammatory flares, patient variability, and client compliance and financial considerations, the 2023 American Animal Hospital Association guidelines emphasize that “treating the allergic dog is not one-size-fits-all” (9). By extension, there is no one-size-fits-all methodology for conducting RCTs in canine AD.
Applying uniform trial methodologies risks overlooking clinically meaningful differences in disease presentation, severity, and treatment response. Standard endpoints may also inadequately capture the broader burden of disease on canine AD patients and their owners, particularly in subgroups with comorbid conditions such as recurrent skin infections. Progress therefore requires flexible study designs that align eligibility criteria, washout rules, and outcome measures with the phenotype under investigation, supported by adaptable protocols and patient-centered endpoints that better reflect real-world heterogeneity. Through such approaches, coupled with ongoing translational research, the veterinary community can accelerate the development of effective therapies that address the diverse needs of the canine AD patient population.