AI peer review for preclinical cancer research

PerfectPaper reviews preclinical manuscripts with a standing team of specialist agents, and lets you add up to three custom agents of your own. This page carries five prebuilt briefs for cancer biology: unit of analysis and pseudoreplication, in vivo experimental rigour, flow cytometry reporting, image quantification, and model-to-human relevance. Each is text you paste into the agent field.

Preclinical papers rarely fail because the statistics are wrong in the abstract sense. They fail because the unit being counted is not the unit that varies, because the design details that make an animal experiment interpretable were never written down, or because a model cannot support the claim being drawn from it.

The five agents

Unit of analysis and pseudoreplication — n counted as cells, tumours or wells when the independent unit is the animal or the experiment. The single most consequential statistical error in this literature, and one that is visible from the text.

In vivo experimental rigour — randomisation, blinding, sample size justification, exclusion criteria, animal sex, tumour volume formula, humane endpoints.

Flow cytometry reporting — gating strategy, controls, viability discrimination, and denominators that shift without notice.

Image quantification integrity — representative images standing in for quantification, unblinded scoring, unstated thresholding, sampling that is never described.

Model-to-human relevance — immune and microenvironment claims drawn from models that cannot support them.

What a preclinical manuscript is reviewed against

A preclinical manuscript is reviewed against three things outside it: the reporting guideline its journal endorses, the minimum-information standard for the assay carrying its central figure, and the biology of the host or system it used. The standing specialist team reads the paper against itself — structure, arithmetic, table consistency, figures, citations, statistics, causal inference. The five agents on this page read it against those external documents.

The documents are specific. The ARRIVE guidelines 2.0 (Percie du Sert et al., PLOS Biology 2020;18(7):e3000410) organise animal reporting into the Essential 10: study design, sample size, inclusion and exclusion criteria, randomisation, blinding or masking, outcome measures, statistical methods, experimental animals, experimental procedures, and results — covered in full at the ARRIVE guidelines. Landis and colleagues, reporting an NINDS workshop in Nature (2012;490(7419):187–191), set four minimum standards behind them: randomisation with the method reported, blinding including allocation concealment and blinded outcome assessment, sample-size estimation computed at design time, and data handling covering stopping rules, inclusion and exclusion criteria, outlier handling and attrition. For cytometry, MIFlowCyt (Lee et al., Cytometry Part A 2008;73A(10):926–930) requires that authors “define qualitative gate descriptors as well as to state denominators used to calculate percentages of events within a gate”. For images, the Journal of Cell Biology rule set out by Rossner and Yamada (2004;166(1):11–15) is that “No specific feature within an image may be enhanced, obscured, moved, removed, or introduced”.

None of those clauses is quoted in a typical methods section. That is the gap the five agents fill: each finding names the missing item, the figure or the strain, rather than reporting that something is unclear.

How custom agents work

Every review can carry up to three custom agents. Each takes a name, instructions up to 6,000 characters, a work type, a skill level, and an optional tool selection — web search, scholarly search, code execution, and vision for reading figures. PerfectPaper supplies the review contract and output format, so the brief describes what to look for rather than how to report it.

The five briefs on this page each fit inside the 6,000-character limit with room to add your own items, and each names its suggested settings on its own page. Tool choice is the setting authors get wrong most often in this cluster. Code execution lets the unit of analysis agent recompute a standard error under the correct n instead of judging arithmetic in prose. Vision lets the image quantification agent read the panel rather than the caption, and lets the cytometry agent see whether a gating figure traces back to all events. Web search and scholarly search matter less here than in clinical trial review, because almost everything these five checks need is inside the manuscript.

Writing your own variant, rather than pasting one of these, is covered in how to write a custom reviewer agent; the full catalogue across fields is at custom AI reviewer agents.

Frequently asked questions

How many custom agents can I add to one review?

Three. PerfectPaper’s standing specialist team already reviews methodology, statistics, causal inference, figures, tables and citations on every manuscript; the three custom agent slots let you add checks specific to your subfield — for a preclinical cancer paper, that means choosing among the five prebuilt briefs on this page rather than writing your own from scratch.

Do these agents replace ARRIVE checklist compliance?

No. The in vivo rigour agent judges whether your design actually supports the causal claim you’re making — a stricter, more contextual read than a checklist — but a journal that requires an ARRIVE checklist still requires you to submit that checklist separately. Checklist compliance and design adequacy are two different questions.

Can an agent actually read my figures, or just the caption?

Only if you enable the vision capability, which is why it matters most for the image quantification agent: without it, that agent sees the caption and the surrounding text, not the panel itself, and a caption saying “representative image” tells it nothing about what the pixels show.

Which agent should I pick for a tumour growth experiment?

Pseudoreplication first, because tumour growth studies routinely count tumours or measurements rather than the animals that generated them; add in vivo rigour next, for randomisation, blinding and the volume formula, since both failures show up in the same experiments and neither is caught by the other agent.

Choosing among them

For most in vivo papers, take pseudoreplication and in vivo rigour first; together they cover the two questions a methods-focused reviewer asks before anything else. Add flow cytometry or image quantification depending on which assay carries your central figure. Model relevance is most valuable for papers making immunological claims, and least valuable for papers whose conclusions stay within the model.

If your central figure is an image panel, give that agent the vision capability so it reads the figure rather than only the caption.

Three slots and five agents mean two are always left out, so choose by what the paper claims rather than by what it is about. A tumour growth study in a syngeneic host claims efficacy and mechanism: pseudoreplication, in vivo rigour, and then cytometry if the mechanism rests on an immune infiltrate. A cell-biology paper with no animals at all still needs pseudoreplication, because independent biological replicates and repeated measurements from one culture are confused as often in dishes as in mice; the second and third slots go to image quantification and model relevance. A checkpoint-blockade paper run in nude mice needs model relevance in slot one, ahead of everything else, because the host cannot contain the phenomenon and no amount of design rigour repairs that.

The unit of analysis is the experiment, not the measurement

Pseudoreplication is counting measurements as if they were independent experiments, and it is among the most common ways significance is inflated in this literature. Six mice with twenty-five cells measured each is n = 6, not n = 150. Standard error falls with the square root of the sample size, so reporting 150 measurements from 6 animals can shrink the standard error by as much as a factor of five and inflate the test statistic by the same amount — the full five only where the variance sits between animals rather than between cells within an animal.

The consequence has been measured. Aarts and colleagues reviewed 314 neuroscience papers, found 53% reported nested data, and their simulation put the probability of declaring a null effect significant at as much as 80% against a nominal 5% (Nature Neuroscience 2014;17:491–496). A p-value computed on cells routinely fails to survive recomputation on animals, from the same experiment, with nothing else changed.

The rule is stated plainly in the British Journal of Pharmacology guidance for authors and peer reviewers (Curtis et al., 2018;175:987–993): “Group size is the number of independent values, so one sample run five times is n = 1, not n = 5”, and, on the canonical case, “Five cells from one mouse given the same treatment is not n = 5, and these five cells should be regarded as technical replicates, with n = 1 consensus value taken forward into statistical analysis.” That journal also sets 5 as the minimum n for a dataset subjected to statistical analysis, so three animals with fifty cells each does not meet the minimum however many measurements it holds — which converts the finding into a sample size problem the moment it is corrected. ARRIVE 2.0 item 1b asks authors to state “The experimental unit (e.g. a single animal, litter, or cage of animals)”, and most manuscripts do not.

Two remedies both work. Average to the independent unit and analyse the means, or fit a mixed-effects model with animal or experiment as a random effect, which uses every measurement while attributing variance to the level it came from. The presentation that survives review shows both levels: plot the 150 cell values lightly, overlay the six per-animal means as larger points, colour-code by experiment, and compute the statistics on the means — the SuperPlot of Lord, Velle, Mullins and Fritz-Laylin (Journal of Cell Biology 2020;219:e202001064). A SuperPlot drawn correctly and analysed at the cell level is still pseudoreplicated, so state in the legend which level the error bars and the p-value were computed at. The reviewer-facing version of this objection, and the wording it arrives in, is at n is not independent.

A mixed-effects model only delivers that fix when its random-effect structure matches how the variance actually entered the data. A random intercept for animal corrects cells nested within animal; it does not correct a design where the treatment itself was applied cage-by-cage, because then cage — not animal — is the level that needs its own random effect, and animal-level random intercepts alone will still understate the standard error. Name the level treatment was applied at before choosing what the model’s random effects should be, not after.

Common questions about pseudoreplication and n

Is n=3 enough if all three come from one culture?

No — three replicates from one culture is n=1, because the independent unit is the culture or the animal it came from, not the measurement taken from it. The British Journal of Pharmacology‘s guidance sets five as the minimum n for a dataset subjected to statistical analysis; three technical replicates from a single dish never meets that minimum, however many values are recorded from it.

My reviewer said n=6 mice is actually n=1 — what does that mean?

A reviewer writes that when all six mice belonged to one experimental run — one cage, one day, one batch of reagent — so the six values read as repeats of a single trial rather than six independent trials. Repeating the whole procedure independently, on separate cohorts or separate days, is what converts n=6 mice into six true replicates a statistic can be computed across.

Can I just average my technical replicates and move on?

Yes — averaging technical replicates to one value per independent unit, then analysing at that level, is one of the two accepted remedies for pseudoreplication, alongside a correctly specified mixed-effects model. Averaging is simpler to defend in a response letter than a mixed model, though it discards the within-unit variance a mixed model would otherwise preserve.

Four design details decide whether an animal experiment is interpretable

Randomisation, blinding, sample size justification and exclusions decide whether an in vivo result can be read as an effect of treatment, and all four are missing from most published work. Macleod and colleagues assessed a random sample of 146 in vivo publications and found randomisation reported in 20%, blinded assessment of outcome in 3%, and a sample size calculation in 0% (“Risk of bias in reports of in vivo research: a focus for improvement”, PLOS Biology 2015;13(10):e1002273). In a further set of 1,173 publications from leading UK institutions, a sample size calculation appeared in 1.4% and inclusion or exclusion criteria in 10.4%.

Blinding is the item that most changes a number, and caliper measurement of tumour volume is its worst case: manual, repeated over weeks, on a tumour whose edge the assessor defines, usually by the person who knows the arm. Bebarta, Luyten and Heard classified 290 animal-study abstracts with two or more groups, presented at five years of Society for Academic Emergency Medicine meetings, and found unblinded studies more likely to report a positive result, at an odds ratio of 3.2 (95% CI 1.3 to 7.7); non-randomised studies gave 3.4 (95% CI 1.7 to 6.9), and studies using neither technique, versus both, gave 5.2 (95% CI 2.0 to 13.5) (Academic Emergency Medicine 2003;10(6):684–687). That is an effect on reported findings comparable in size to many of the treatment effects being reported.

The fix is a sentence, not an experiment. What a reviewer writes: “The method of randomisation is not stated. Please describe how the allocation sequence was generated, when allocation occurred relative to tumour implantation, and whether the person administering treatment had access to the sequence.” What to write instead: “On day 7 after implantation, when mean tumour volume reached 100 mm³, 40 mice were ranked by tumour volume, divided into 10 strata of 4, and randomised within stratum to four arms using the NC3Rs Experimental Design Assistant; cage cards were coded by an investigator who took no further part in the experiment.”

Two reporting details specific to tumour work sit alongside those four. The volume formula must be named, because the common ones disagree: the modified ellipsoid formula, volume = length × width² / 2, and the ellipsoid formula, volume = π/6 × length × width × height, return different numbers from the same tumour. And the humane endpoint must be stated with its criterion — Workman and colleagues’ guidelines for the welfare and use of animals in cancer research (British Journal of Cancer 2010;102(11):1555–1577) state that for an animal carrying a single tumour the mean diameter “should not normally exceed 1.2 cm in mice or 2.5 cm in rats, or 1.5 and 2.8 cm, respectively, for therapeutic studies”, so volumes implying diameters well past a stated limit are a reporting inconsistency a reviewer will raise. A mean tumour volume curve plotted past the day control animals began to be removed is a mean over survivors, and it flattens because the largest tumours have left the dataset. Note also that a sample size defended after the fact answers no question a reviewer asked, because a post-hoc power calculation computed from the observed effect is a restatement of the p-value; the quantity that matters at design time is statistical power.

Randomising individual mice still leaves the cage unaddressed as a source of shared variance, and what to do about it depends on how the treatment reaches the animal. Littermates housed together share diet, handling, light cycle and cage microbiome. Where the treatment is delivered to the whole cage — in the chow, in the drinking water, by inhalation — the cage is the experimental unit, not the mouse, and ARRIVE 2.0 says so directly: “the experimental unit may be the cage or the litter (e.g. a diet administered to a whole cage, or a treatment administered to a dam and investigated in her pups)”. Ten cages of four mice is then n = 10, and a manuscript reporting n = 40 has repeated the pseudoreplication error one level up.

Where each animal is dosed individually, the remedy runs the other way, and this is the part authors most often get backwards. Assigning whole cages to arms is what confounds cage with treatment: every animal in an arm then shares one cage’s microbiome and one cage’s position on the rack, and the design cannot separate the two. Putting every arm in each cage and randomising within it makes cage a block rather than a confounder — ARRIVE describes blocking as splitting the experiment into sub-experiments in which “treatments are randomised to experimental units within each block” — which removes the cage effect from the treatment comparison and keeps the mouse as the unit. Include the blocking factor in the analysis as well as the allocation. The exception is contamination: with an oral compound that survives coprophagy, or in microbiome work, cage-mates cannot be held to different arms, and cage-level allocation with the cage counted as the unit is the honest design.

Questions about in vivo study design

Do I need to randomize and blind a simple tumor growth study?

Yes — randomisation and blinding are two of ARRIVE 2.0’s Essential 10 items, and Macleod and colleagues found both reported in fewer than a quarter of the 146 in vivo publications they assessed. A “simple” tumour growth study is exactly where blinding lapses most, because caliper measurement makes tumour volume the outcome most sensitive to an assessor who knows the treatment arm.

Which tumor volume formula should I use — length×width² or the ellipsoid formula?

Both formulas are legitimate, but only if you name which one you used and hold it constant: the modified ellipsoid formula (length × width² / 2) and the true ellipsoid formula (π/6 × length × width × height) return different numbers from the same tumour. Switching formulas mid-study, or leaving the formula unstated, makes every reported volume in the manuscript unverifiable.

Reviewer 2 wants a power calculation I never ran before starting the experiment — what do I say now?

A post-hoc power calculation, computed after the data are already in hand, restates the p-value and answers no question the reviewer actually asked — say so directly rather than running one. State plainly that the sample size was not pre-calculated, report the effect size with its confidence interval, and describe what a properly powered follow-up experiment would need.

Cytometry percentages fail on their denominators

A flow cytometry percentage is uninterpretable without its parent population, and the parent is the item most often lost between the analysis software and the figure. A population that is 2% of live cells might be 20% of CD45+ cells; the same measurement reported against different parents gives numbers an order of magnitude apart, and neither is wrong. MIFlowCyt has required both the gate descriptors and the denominators since 2008. The loss is mechanical rather than careless: inside the software the parent sits directly above the child in the hierarchy, and the ambiguity appears the moment the plot is exported and the axis is labelled % CD8+.

Three further items decide whether the percentages mean anything. Viability discrimination comes first, because cells with compromised membranes bind antibody conjugates non-specifically and can shift a rare population’s frequency on their own — the reason amine-reactive fixable viability dyes became standard practice (Perfetto et al., Journal of Immunological Methods 2006;313(1–2):199–208), and the reason forward and side scatter alone will not do. Second, controls: an isotype tube estimates non-specific binding of a matched immunoglobulin, while a fluorescence-minus-one tube estimates the spread contributed by the rest of the panel, and in a polychromatic panel the second dominates. Third, the gating figure itself. MIFlowCyt’s requirement is directional and absolute — “The overall gating strategy shall be traceable up to the set of all events” — so a supplementary panel that begins at “lymphocytes” does not satisfy it, because the reader cannot see how lymphocytes were defined. Nature Portfolio’s Reporting Summary turns the same requirement into a confirmation checkbox.

Isotype and fluorescence-minus-one controls answer different questions, and a panel that reports only one of them is usually reporting the wrong one for its actual source of error. An isotype control addresses nonspecific binding of the antibody itself; it says nothing about spectral spillover from neighbouring fluorochromes, which is the dominant source of gating uncertainty once a panel passes about six colours. A manuscript defending a rare population’s boundary with an isotype control alone, in an eight- or ten-colour panel, has controlled for the smaller of its two error sources.

Common questions about flow cytometry reporting

Why does my CD8+ percentage change depending on what I gate on?

A flow cytometry percentage has no meaning without its parent population, which is why the same measurement changes with what you gate it against — 2% of live cells can be the same population as 20% of CD45+ cells. MIFlowCyt has required both the gate descriptors and the stated denominator since 2008; put the parent population in every axis label and legend.

Isotype control or FMO control — which do I actually need?

In a polychromatic panel, use a fluorescence-minus-one (FMO) control to set your gates, not an isotype control. An isotype tube only estimates non-specific binding of a matched immunoglobulin; an FMO tube estimates the spread every other fluorochrome in the panel contributes to your channel of interest, which is the larger source of gating error once a panel runs past about six colours.

Representative images are not quantification

An image panel supports a claim only when the manuscript states how many fields, sections and animals stand behind it, and that sampling statement is one of the first things a reviewer asks for when it is missing. The recurring problem is not image manipulation. That has been measured and it is the smaller problem: Bik, Casadevall and Fang screened 20,621 published papers and found 3.8% contained problematic figures, with at least half of those showing features suggestive of deliberate manipulation (mBio 2016;7(3):e00809-16). Undescribed sampling is not 3.8% of manuscripts.

Where the sampling effort should go is a solved problem. Gundersen and Østerby answered it in “Optimizing sampling efficiency of stereological studies in biology: or ‘do more less well!’” (Journal of Microscopy 1981;121(Pt 1):65–73): because between-animal variance usually dominates the total, precision is bought far more cheaply by adding animals than by adding fields within an animal. Twenty fields from three mice is a worse experiment than five fields from twelve mice, at similar bench time — and the first design is also the one that produces a pseudoreplicated n of 60. Counting objects from single two-dimensional sections carries its own size-dependent bias, which the disector (Sterio, Journal of Microscopy 1984;134(Pt 2):127–136) was designed to remove.

Two claims in this area need more than a picture. A colocalisation claim is an overlap claim, and Pearson’s correlation coefficient does not test it: Pearson’s measures whether two channels’ intensities co-vary, while Manders’ coefficients M1 and M2 measure what fraction of each channel’s signal overlaps the other (Dunn, Kamocka and McDonald, American Journal of Physiology — Cell Physiology 2011;300(4):C723–C742). And a display adjustment needs the Journal of Cell Biology rule applied: linear adjustments equally across the whole image and equally across compared panels, nonlinear adjustments such as gamma changes disclosed in the legend, and quantification taken from the raw file rather than the display copy. Scoring by eye, unblinded, is the last item — the same blinding problem as in vivo, in a setting where the eye assigns the number directly.

An automated or machine-learning scoring pipeline changes who does the counting, not whether the sampling behind it needs disclosing. A model trained on an unrepresentative set of fields inherits the same undersampling problem as a human counting too few fields — silently, because the output looks quantitative either way. The sampling statement a reviewer asks for applies to the fields fed into the pipeline, not only to fields counted by eye.

The model has to contain the phenomenon

A model claim fails when the host lacks the compartment the abstract describes, and no amount of design rigour repairs it. Begley and Ellis, describing Amgen’s attempt to reproduce 53 landmark preclinical oncology papers in Nature (2012;483:531–533), reported that the scientific findings could be confirmed in 11% of them. Model choice is not the only reason a result fails to travel, but it is the reason that survives perfect data.

The compartments are specific and checkable from the strain name. Athymic nude mice lack mature T cells; SCID mice lack T and B cells but retain NK and myeloid cells; NSG mice lack T, B and NK cells and carry residual myeloid cells with impaired function. A checkpoint claim, an antibody-dependent cellular cytotoxicity claim or a complement-dependent lysis claim made in a host missing the relevant cells is unsupportable regardless of the p-value. Site is a separate finding from strain: a syngeneic MC38 tumour in a fully immunocompetent C57BL/6 mouse still sits under the skin, and the lymphocyte populations recovered from a flank tumour are not those recovered from a colon tumour. Patient-derived xenografts carry a provenance problem of their own — Ben-David and colleagues monitored copy number alterations in 1,110 PDX samples across 24 cancer types (Nature Genetics 2017;49:1567–1575) and found alterations accumulating rapidly during passaging, so a late-passage PDX is a model whose divergence is undocumented unless passage number and a genomic comparison are reported.

A humanised strain — an immunodeficient mouse engrafted with human haematopoietic stem cells or PBMCs — is sometimes offered as the fix for a missing human immune compartment, but engraftment is partial and uneven across lineages: reconstitution typically skews toward human T cells, with weaker and slower myeloid and NK recovery. A humanised-mouse claim about a specific human lineage still needs the same compartment check as a claim in NSG or SCID mice, not a pass on it, because the strain that fixed one missing compartment can still be missing another.

How to detect these in your own manuscript before submitting

Five checks find most of what these agents find, and each takes under an hour with the manuscript open.

Write down what every stated n counts. Go figure by figure. For each n, name the thing being counted — cells, wells, fields, tumours, animals, independent experiments — and the number of times the treatment was independently applied. Any figure where the first number exceeds the second is a candidate, and the check is arithmetic rather than judgement.

Reconcile the animal numbers. Animals ordered, animals implanted, animals randomised, animals in each figure legend, animals in the survival curve. A study reporting 40 randomised and 36 analysed has 4 animals whose exit needs a count, a group and a pre-specified reason.

Read every percentage in a cytometry figure for its parent. If an axis says % CD8+ and the text does not say of what, add the denominator to the legend now rather than in a response letter.

State the sampling behind every image panel. Fields per section, sections per animal, animals per group, how fields were chosen, who scored them and whether that person knew the group.

Name your host’s missing compartment, then reread your abstract against it. If the abstract makes an immune claim the strain cannot support, the sentence to change is in the abstract. This is also what overclaim checking does across the whole manuscript.

What reviewers write when this is mishandled

Reviewers rarely name the class of defect. They write the specific version, and these are the comments that hold preclinical papers in revision.

“The n of 150 appears to be cells rather than animals; please clarify the experimental unit and reanalyse at that level.” “It is not stated how animals were allocated to groups.” “Was the investigator measuring tumours blinded to treatment?” “Please state the formula used to calculate tumour volume.” “Figure 3 shows representative images; how many fields and how many animals were quantified, and by whom?” “The percentage in Figure 4B has no stated parent population.” “A gating strategy figure is required in the Supplementary Information.” “The authors conclude that the compound acts through CD8+ T cells, but the experiment was performed in athymic nude mice.” “Colocalisation is claimed on the basis of Pearson’s coefficient alone.” “Three animals per group with no sample size justification cannot support the conclusion drawn.” “The mean tumour volume curve continues past the point at which control animals were removed.”

Almost every one of these is answerable from data the authors already hold, which is the argument for finding them before submission rather than in a response letter. The exceptions are the model objection and the blinding objection, which sometimes cannot be answered at all. The objection that most often follows a corrected unit of analysis has its own page: the experiment was not replicated.

When the obvious remedy is unavailable

Most findings in this cluster arrive after the animals are gone, and the remedy is then to bound the claim rather than to restate it.

The correct n makes the result non-significant. Report it that way and say what the experiment now supports — usually a direction and an effect size with a wide interval, rather than a demonstrated difference. A result reported at the right unit with an honest interval survives review; the same result at the wrong unit does not survive a reader who does the division.

Blinding was not performed and the tumours are measured. State that measurement was unblinded, name the direction of the expected bias, and where an objective secondary readout exists — bioluminescence, terminal tumour weight, an imaging endpoint — report it alongside the caliper data as a partial control on the assessor.

The syngeneic repeat is not possible. State the compartment. “In athymic nude mice, which lack mature T cells, compound X reduced tumour growth, indicating a T cell independent component of activity” is a stronger sentence than a suppressed immune claim, because it converts a limitation into a specification about mechanism. Move the immune hypothesis into the discussion, labelled as a hypothesis, and name the experiment that would test it.

The raw images are gone and only the figure remains. Report the sampling that was used, state that quantification was performed on the panels available, and avoid any measurement the display copy cannot support — intensity comparisons above all.

The exclusion criterion was decided after the data were seen. Say so, report the analysis with and without the excluded animals, and let the reader see the difference. A limitations section that names the direction and magnitude of each defect is stronger than one that lists them.

What this page is not for

These five agents review original research articles reporting preclinical animal and cell-biology studies. They are not the right agents for a clinical trial report, a systematic review or meta-analysis, an epidemiological cohort, a qualitative study, or a protocol paper with no results. A first-in-human or dose-escalation manuscript belongs with the clinical trial agents; a paper whose central claim rests on a sequencing run needs multiple testing in omics and batch effects instead; a preclinical paper arguing that a compound merits clinical development also wants translational dose relevance.

PerfectPaper is expert-led and AI-assisted: the review it produces is a pre-submission read of a manuscript, not a substitute for journal peer review, and none of these agents can rerun an experiment, inspect a raw image file that was never deposited, or recover a randomisation that never happened. What they do is find the objections a reviewer would raise while you can still act on them. The general case for the standing team is at AI peer review.

Related

Pseudoreplication · In vivo rigour · Flow cytometry reporting · Image quantification · Model relevance · Custom AI reviewer agents

PerfectPaper reads the methods, the figure legends and the results of a preclinical manuscript together, and reports where the stated n, the described design and the model used stop supporting the claim in the abstract.

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