These Bitches Deserve Better
I felt compelled to write a more detailed narrative of what I believe has been a failure in understanding from practitioners, poor peer-review processes, and to hopefully atone for my sins in perpetuating my personal misunderstanding and poor critical analysis of maropitant as an “analgesic” in the past- where I am still haunted by my words even today. The push toward opioid-free and opioid-sparing anesthesia in veterinary medicine is not unreasonable. In fact, it’s well supported in human literature and in my personal experience has been a positive change. The concerns driving it (regulatory burden, diversion risk, species-specific adverse effects, and genuine logistical constraints in general practice) are legitimate and deserve thoughtful clinical responses. What is not acceptable, however, is replacing one sufficiently examined drug with another insufficiently examined drug, calling it evidence-based, and publishing it in a peer-reviewed journal. We have been through this before with tramadol and gabapentin, people! That is not progress. That is reassurance marketed as science for one reason or another.
Maropitant (Cerenia®; Zoetis) has, over the past decade, accumulated a growing body of literature suggesting it reduces the minimum alveolar concentration (MAC) of volatile anesthetics during visceral stimulation. That finding is real, modestly reproducible, and reasonably well characterized within its specific context. It is also being systematically over-interpreted. BUT, please understand I am not saying to not use it- in fact, the contrary. I prefer it for all my patients with ondansetron. However, we (the Nerds) have been alerted to two more recent papers on this conversation. A paper published in The Veterinary Journal in 2026 — Figueirinhas et al. (Evaluation of maropitant’s analgesic and tissue relaxation effects during ovariohysterectomy in bitches)— provides an instructive case study in exactly how that over-interpretation happens, what it looks like when it reaches print, and why it carries clinical consequence. The other paper has many of the same concerns and will be briefly discussed later in this piece.
Clarifying Terminology
Before evaluating what this study found, the key term requires definitions. "Analgesia" is not the same as "MAC reduction." This distinction is not pedantic. It is the entire issue.
MAC measures the alveolar concentration of an inhalant anesthetic at which 50% of subjects do not move in response to a standardized noxious stimulus aka a surgical plane of anesthesia. When a drug reduces MAC, it means less inhalant is required to suppress movement. That reduction can arise from true analgesia, from sedation, from CNS depression, from altered autonomic tone, or from combinations of all four. As Grimm et al. (2024) note in Lumb and Jones Veterinary Anesthesia and Analgesia (6th ed.), MAC determination is a useful research tool because it provides a controlled environment and reduces variability, but it does not, on its own, confirm analgesic activity in subjects.
Boscan and colleagues (2011), whose work is the most-cited foundation for maropitant's MAC-sparing properties, stated this explicitly in their original paper: "If a particular drug reduces the MAC, further studies are required to determine the true analgesic effect of the drug in awake subjects." This caveat appears in the paper that Figueirinhas et al. (2026) cite to support their conclusions. It does not appear in their discussion. If that wasn’t a citation error it’s certainly an interesting choice.
Design Flaw?
Every animal in this study received dexmedetomidine at 3 µg/kg intramuscularly. Dexmedetomidine is an α₂-adrenergic agonist with well-established intrinsic analgesic activity at both spinal and supraspinal sites (Grimm et al., 2024; Duke-Novakovski et al., 2016). In the methadone group, this was combined with a full µ-opioid agonist that also carries NMDA antagonist properties. In the maropitant group, dexmedetomidine stood alone as the only definitive pharmacologically analgesic drug in the protocol.
What this study compares is: dexmedetomidine plus opioid versus dexmedetomidine without opioid. Maropitant is structurally a confounder in this design not the independent variable. The conclusion that maropitant "provides effective analgesia" does not follow from a design in which a legitimate known analgesic drug was present in 100% of subjects throughout.
Any analgesic-like outcome observed in the maropitant group could reflect dexmedetomidine alone. The study provides no mechanism to separate these contributions. This is not a minor methodological footnote and it was never addressed.
The Heart Rate Paradox They Never Resolved
The maropitant group had significantly higher heart rates at every single recorded time point. From T0 (88.5 vs. 61.1 bpm, before a single incision) through T6 at skin closure (71.4 vs. 63.3 bpm). These are not subtle differences. At T0, after premedication only, the maropitant group was running 27 beats per minute faster than the methadone group. The authors attribute this to methadone's well-known µ-opioid-mediated bradycardia, which is fair.
The problem is that the study (and other similar papers) also uses heart rate and mean arterial pressure as its primary intraoperative indicators of nociception. The rescue analgesia threshold was a ≥25% increase from the preceding five-minute baseline. If heart rate is your nociceptive surrogate… and this paper uses it as exactly that… then the group with consistently higher heart rates throughout the entire procedure is, by the study's own logic, experiencing more nociceptive and sympathetic drive. It’s also notable that patients in both groups were started on inhalant at 3% and subsequently adjusted based on clinical signs. Of note, the percentage of gas was not noted in this study leaving a hanging question of total and chronic dosing of the inhalant between the two groups.
The conclusion dismisses the elevated vitals by describing the elevated heart rates in the maropitant group as reflecting "lighter sedation rather than inadequate analgesia." That may be true. But the paper cannot simultaneously argue that higher heart rates indicate only lighter sedation and that postoperative behavioral differences indicate better analgesia. These interpretations to me feel applied opportunistically.
There is also a structural inequity embedded in the rescue protocol. A 25% increase from a baseline of 88 bpm triggers rescue at 110 bpm. A 25% increase from 61 bpm triggers rescue at 76 bpm. These are not equivalent thresholds applied to equivalent patients. In my opinion, from what I understood in the paper is the system was architecturally biased against detecting inadequate analgesia in the maropitant group, and this is never acknowledged.
Sidenote: Nociception is the neural processing of a noxious stimulus with the afferent signal traveling from tissue, through the spinal cord, to the brain. It is a physiological event. It does not require consciousness. An anesthetized patient can mount a full nociceptive response via autonomic activation, hormone release, spinal cord sensitization without any subjective experience of pain whatsoever.
Analgesia is the reduction or elimination of the perception of pain. Technically, it refers to a conscious experience. Under general anesthesia, by definition, there is no conscious perception, so "analgesia" in the strict sense cannot be directly measured in an anesthetized patient.
This creates the fundamental problem in anesthesia research and most, if not all the maropitant papers: we cannot measure analgesia under anesthesia. We can only measure surrogates of nociception.
Emesis and nausea add to the pain experience!
This may be the most important concern in the paper, and it is never mentioned. Not in the limitations section. Not in passing. Not at all. Methadone, like all µ-opioid agonists administered by the intramuscular route, can cause nausea in dogs. Maropitant, as its primary pharmacological function, prevents opioid-induced nausea and vomiting (Hay Kraus, 2014; American Animal Hospital Association, 2024). Dogs experiencing subclinical nausea will vocalize, resist interaction, display altered facial expressions and generally behave in ways that score poorly on any behavioral pain scale.
The lower postoperative scores in the maropitant group - the single outcome the paper builds its entire conclusion upon - may have nothing to do with analgesia, and were in fact not statistically significant. They may simply reflect the fact that those dogs were not nauseated (primary effect is antiemetic) while the methadone-group dogs were. This is not an exotic alternative hypothesis. It is the most parsimonious explanation for the observed difference between groups, and it maps directly onto maropitant's primary, well-established mechanism of action.
The Abstract Does Not Accurately Represent the Data
The abstract states that maropitant-treated dogs showed "lower postoperative pain scores at 0, 1, and 2 h." Table 7 shows that at one-hour post-extubation, pain scores were 0.818 (maropitant) versus 0.811 (methadone). At two hours: 0.818 (maropitant) versus 0.676 (methadone). The maropitant group was numerically worse at both timepoints.
The abstract also states, "reduced need for rescue analgesia." Table 4 shows intraoperative rescue rates of 0.432 (maropitant) versus 0.394 (methadone), p= 0.394. That is not significant by any conventional threshold. It was described as a finding.
The abstract describes a highly subjective measure of ovarian exteriorization as "easier" in the maropitant group. Table 4 shows left ovarian traction scores of 2.649 (maropitant) versus 2.545 (methadone), is not significant, and with maropitant scoring numerically higher, meaning more resistance. There was no significant difference on either ovary. An abstract that misrepresents its own tables is not a minor issue since many practitioners will only read and extrapolate from the abstract.
Also, there is a huge glaring error in the abstract compared to the body of the paper. In the abstract, it is stated, “postoperative pain was evaluated using the CMPS-SF scale.”, which stands for “Short Form of the Glasgow Composite Measure Pain Scale”, while in the body of the text it states, “Postoperative pain was assessed using the Colorado State University Canine Acute Pain Scale (CSU-CAPS)”. Which was it? If it was in fact the CSU-CAPS the study is void as this is not a fully validated pain scoring instrument.
Additionally, this study noted, “Sedation levels were clinically assessed to ensure safety and adequate conditions for induction, but no formal scoring system was applied, since it was not considered essential for the evaluation of analgesic efficacy, which was the primary objective of the study.” I disagree. Sedation depth directly shapes behavior, and behavior is what every pain scale is measuring. If your two drug protocols produce even subtly different sedation profiles, and these ones did… you haven't controlled for that variable, you've just ignored it. In an underpowered study where small differences between individual animals can move the numbers, that's not a minor methodological footnote. Additionally, breed disposition and patient personality are becoming more prevalent in our assessments of pain in animals, not to mention this was something scored in other similar studies.
The Blinding Concerns
The paper describes a double-blind design. Maropitant has a characteristic sulfurous (band aid) odor- that I love. It was administered subcutaneously in the cervical region. Methadone was administered intramuscularly in the hind limb, combined with dexmedetomidine in the same syringe. No masking protocol was described, or a sham injection in the methadone group was described. The premedication administrator was excluded from evaluations thankfully, but the evaluators encountered these animals directly after premedication in the recovery and monitoring phases.
Between the route difference, the injection site difference, and the odor, the conditions for incidental unblinding were present and unmitigated. The study is described as double-blind. It was, at best, partially blinded under conditions that systematically favored the maropitant group appearing better behaved.
The Dosing Discrepancy
The study invokes Boscan et al. (2011) repeatedly to support its analgesic claims while leaving out con papers on maropitant’s non analgesia- both in animals and its human cousin aprepitant. Boscan's protocol used intravenous loading doses of maropitant (1 mg/kg IV over 10 minutes) followed by a continuous rate infusion (30 µg/kg/h) targeting plasma concentrations of approximately 90 ng/mL, with a higher-dose arm targeting 150 µg/kg/h. That is a pharmacologically deliberate, plasma-concentration-controlled protocol designed for a MAC determination study.
The current study administered 1 mg/kg subcutaneously as a one-time premedication dose. Subcutaneous absorption is slower, variable, and produces lower and delayed peak plasma concentrations compared to IV administration (Benchaoui et al., 2007, as cited in Figueirinhas et al., 2026). No plasma drug concentrations were measured. No CRI was used to maintain consistent drug levels during the nociceptive period of interest. No dose-response curve and plasma concentration corroborated with a validated pain scoring instrument or nociceptive stimuli.
In my reading of the paper the current authors cite Boscan's findings as if the two protocols are pharmacologically equivalent. They are not. This is a citation used as institutional decoration rather than scientific support.
The Study Was Underpowered by Its Own Calculation
Listen, most, if not all veterinary studies are underpowered and I generally leave this piece alone when reviewing a paper. However, this paper mentioned powering and then had an error. The priori power analysis, cited in the methods section, estimated 68 animals per group were required to achieve 80% power at α = 0.05. “Based on previous literature and pilot data, a sample size of 68 animals per group was estimated to provide a power of 80%...”, compared to “Seventy-two healthy bitches were randomly assigned to receive dexmedetomidine with either methadone (Group M, n =34) or maropitant (Group MAR, n =38)”. The study enrolled 38 and 34 in each group, not 68. This is approximately half the required sample per group.
The Comparator Was Inappropriate
Maropitant was compared head-to-head with methadone as the primary analgesic in a surgical protocol. This is not a design question. It is a conceptual one. This was not a cleaner non-inferiority study comparing two different opioids or NSAIDS. No serious interpretation of the available evidence positions maropitant as a standalone opioid replacement. Its proposed clinical role, even in the most enthusiastic literature, is as an adjunct within multimodal protocols (Marquez et al., 2015; Boscan et al., 2011). Duke-Novakovski et al. (2016), in the BSAVA Manual of Canine and Feline Anaesthesia and Analgesia (3rd ed.), are explicit that no single agent constitutes adequate perioperative analgesia for procedures involving visceral manipulation.
The appropriate question, the one this study should have asked, is whether adding maropitant to a standard protocol improves outcomes compared to the standard protocol alone. That is a useful clinical question with a potentially useful clinical answer. That is not what was tested.
On the Clinical Significance of a 15–24% MAC Reduction (a relevant note)
While a specific claim of an actual percentage was not made in this study, in a separate study with a similar aim did claim a specified reduction and I have concerns. Assessment of Maropitant Citrate Effectiveness as an Intraoperative Analgesic Through Monitoring Parasympathetic Tone Activity in Female Dogs Undergoing Ovariohysterectomy
The sevoflurane MAC reductions reported in this study and across the broader maropitant literature fall within a 15–24% range. In practical terms, this translates to adjusting the vaporizer from 3% to approximately 2.3–2.6%.
This requires context. Sevoflurane has a blood:gas partition coefficient of 0.65, which facilitates relatively rapid alveolar equilibration in a rebreathing circuit. However, alveolar concentration and brain tissue effect-site equilibration are not synonymous. The small magnitude of the MAC difference, combined with the brief duration of ovarian traction as an event, means clinically meaningful depth differences may not have fully manifested at the tissue level before the stimulus ended. As Grimm et al. (2024) discuss, inhalant pharmacokinetics in the clinical setting involve equilibration across multiple tissue compartments, and subtle adjustments to delivered concentration require time to produce proportional changes in CNS effect-site concentration. The equilibration also needs to consider mechanical differences with a rebreathing versus nonrebreathing system and even circuit size compared to the amount of time measured for data point collection. A finding from a controlled MAC determination study where adequate equilibration time is built into the protocol design does not automatically translate to the dynamic, time-compressed conditions of clinical ovarian traction. A 15% reduction in a number that was never precisely validated for individual animals is a modest finding. The fact that it is statistically significant does not make it clinically transformative.
The Propofol
The maropitant group required significantly more propofol for induction (5.08 vs 2.46 boluses). This higher propofol exposure does not seem to be addressed as a variable. Propofol produces greater cardiovascular depression and vasodilation, explaining the lower MAP seen in the maropitant group (which the authors attribute to dexmedetomidine's biphasic effects). My question is since we know prolonged CNS depression is seen into the early intraoperative period, potentially influencing all subsequent parameter comparisons- again what’s up with that high heart rate in the maropitant group? Overall, this seems to represent an uncontrolled variable with downstream effects on the primary outcomes
The Practical Consequence
Opioid-free and opioid-sparing protocols are actively being developed in general practice, and maropitant is increasingly named within them as an analgesic component rather than as an antiemetic adjunct. When a clinician reads an abstract - and most will read only the abstract - they encounter the sentence: "Maropitant provides effective analgesia."
The context that this claim rests on a design that cannot isolate maropitant's contribution, a compromised blinding protocol, a postoperative finding more parsimoniously explained by antiemesis, an underpowered sample, and an abstract that misrepresents multiples of the claimed outcome timepoints - that context does not survive the abstract.
The American Animal Hospital Association anesthesia guidelines, the WSAVA pain guidelines and any contemporary anesthesia references consistently frame multimodal analgesia as standard of care for surgical patients. The multimodal framework works because each component contributes through a distinct, additive mechanism. Substituting a drug whose primary mechanism is antiemetic for one whose primary mechanism is analgesic - and then calling the substitution equivalent - is not multimodal analgesia. It is multimodal labeling. There is a painstaking difference.
Kinobe & Miyake (2020) Evaluating the anti-inflammatory and analgesic properties of maropitant: A systematic review and meta-analysis, is not cited anywhere in Figueirinhas et al. (2026). Not in the introduction. Not in the discussion. Not in the limitations. A 2020 systematic review and meta-analysis- published in the same journal, that explicitly concluded maropitant has no analgesic effect was entirely absent from this paper! That is not a minor citation gap. A literature review for a 2026 paper on maropitant's analgesic properties that missed a PRISMA-compliant meta-analysis on maropitant's analgesic properties is either a failure of the literature search or a failure of disclosure. Peer reviewers should have caught it. They did not.
What makes this particularly pointed is that Kinobe & Miyake's conclusion is precise: maropitant reduces MAC, and that MAC reduction does not translate into analgesic effect.
What Maropitant's Role Actually Is
Let me be precise. There is credible evidence that maropitant, when properly dosed and administered via appropriate route and concentration, reduces inhalant anesthetic requirements during visceral stimulation. That is a clinically useful property. It likely reflects NK-1 receptor-mediated modulation of visceral nociceptive transmission at the spinal level. As an adjunct, layered onto an established opioid, opioid sparing, or locoregional technique, it may contribute meaningfully to visceral analgesia and improve postoperative comfort through its antiemetic action.
That is not nothing. It may, in fact, be quite valuable when deployed correctly within the right protocol. But, the use described in this study isn’t it! And a drug that does something useful in the right context does not benefit from being oversold into a role it cannot sustain by readers who are not evaluating the literature critically during their already busy day.
There is a pattern worth naming directly that started long before this paper.
A drug with a real but narrow mechanism of action accumulates a literature of small, underpowered, poorly controlled studies, and makes claims on something not even researched. Each study adds a slight increment of plausibility. Abstracts describe the findings with more confidence than the underlying data warrant. Subsequent papers cite previous papers without revisiting foundational assumptions. The clinical community, navigating regulatory burdens around controlled substances and genuine logistical challenges in practice, finds a narrative that meets a need. And gradually, without any single moment of consensus, an antiemetic becomes an analgesic. This is how publication incentives, institutional pressures, and confirmation bias work together to produce a literature that looks more settled than it is. It is a systems problem, not a character problem.
What mitigates it is the same thing that always mitigates it: clinicians who read beyond the abstract, who understand what a study design can and cannot demonstrate, who recognize when a surrogate outcome has been promoted into a primary claim, and who ask the simple and uncomfortable question - does the evidence actually support what the conclusion says?
In this case, the answer is no. Not because the hypothesis is implausible. Not because maropitant has no value- like I said, I give that shit to everything. But because the study designed to test the hypothesis was not capable of answering the question it claimed to answer — and proceeded to answer it anyway. That distinction is not minor. In anesthesia, where the margin between comfort and inadequate pain control is measured in the patient in front of you, it matters considerably.
