The following points describe the key characteristics that must be included in any research design to assess the internal validity, reliability, and potential for reproducibility of scientific findings. Many of these recommendations have been discussed in various venues (e.g., ARRIVE guidelines; Freedman et al., 2017; Kilkenny, Browne, Cuthill, Emerson, & Altman, 2010; Munafo et al., 2017; Weissgerber, Garovic, Winham et al., 2016; Weissgerber, Milic, Winham, & Garovic, 2015), and some might only be appropriate to specific sciences. However, we feel that inclusion of these criteria, when applicable, into research manuscripts will improve rigor and transparency of the experimental design and statistical approaches.

An appropriately written section describing the experimental subjects must include a statement of ethical approval (Institutional Review Board approval for human research or Institutional Animal Care and Use Committee approval for animals), followed by the total number of participants involved in each experiment. The authors must also include a clear description of the inclusion and exclusion criteria, which should be prespecified prior to the start of the experiments. Reporting the number of experimental units (i.e., subjects, animals, cells) excluded as well as the reason for exclusion is necessary to prevent the researcher from introducing selection bias that favors positive outcomes and distorts true effects (Holman et al., 2016 ). Crucially, studies involving human subjects must not reveal individual identifying information but must contain a full description of the participants’ demographics as variations in the demographics can lead to confounding variables if not appropriately controlled. When designing an experiment, one must also account for sex as a biological variable (see below). One should carefully review the extant literature to determine whether sex differences might be observed in the study and, if so, design and power the study to test for sex differences. Omitting this step could compromise the rigor of the study (Clayton, 2016, 2018 ).

The methods section of each published study begins with a description of the experimental unit; however, in many cases, the information provided falls short. The experimental units are the entity that is randomly and independently assigned to the treatment conditions (e.g., human subject, animal, littler, cage, fish tank, culture dish, etc.) (Lazic, Clarke‐Williams, & Munafo,). The sample size is equal to the number of experimental units. In considering the sample size, one must ensure that the experimental units are independently allocated to the experimental condition, the application of the condition is applied independently to the unit, and the experimental units do not influence one another (Lazic et al.,). A significant concern in cell biology is determining whether cells or sections, for example, can be considered an experimental unit. In cases where an animal is treated and subsequent testing occurs postmortem (e.g., immunohistochemistry or electrophysiology), then the histological sections, neurons per section, spines per neuron, tumor cells per section etc. are all subsamples of the experimental unit, which is the animal, and should be considered an n of 1 (Galbraith, Daniel, & Vissel,; Lazic et al.,). If data are not independent, one strategy is to analyze clustered data (e.g., convert the replicates from a single subject into a single summary statistic (Galbraith et al.,). Alternatively, there are also procedures to accurately model the true variability in data sets using modern statistical techniques (e.g., handling nested data such as cells/animals, littermates) (Wilson, Sethi, Lein, & Keil,). As Stanley Lazic so eloquently concluded in his recent paper (Lazic,):

Choices made by investigators during the design and execution of experiments can introduce bias, which may result in the authors reporting false‐positives (Kilkenny, Browne, Cuthill, Emerson, Altman, & Group, 2010 ; Kilkenny et al., 2009 ; Landis et al., 2012 ). For example, when investigators are aware of which animals belong to one condition or know that a given treatment should have a specific effect, or human subjects become aware of the conditions they are in, the researchers and participants may inadvertently be biased toward specific findings or alterations in a specific behavior (Karanicolas, Farrokhyar, & Bhandari, 2010 ; Schulz & Grimes, 2002 ). To reduce bias in subject and outcome selection, the authors should report randomization and blinding procedures (Festing & Altman, 2002 ). Implementing and reporting randomization and blinding procedures is simple and can be followed using a basic guide (Karanicolas et al., 2010 ; Smith, Morrow, & Ross, 2015 ), but to reduce bias, it is essential to report the method of participant randomization to the various experimental groups as well as on random sample processing and collection of data (Kilkenny, Browne, Cuthill, Emerson, Altman, & Group, 2010 ; Landis et al., 2012 ). Moreover, investigators should report whether experimenters are blind to the allocation sequence and also, in animal studies, report whether controls are true littermates of the test group (Galbraith et al., 2010 ). Similarly, once the investigator is blind to the conditions, they should remain unaware of the group in which the subject is allocated and the assessment outcome (Landis et al., 2012 ). Blinding is not always possible. In these cases, procedures to standardize the interventions and outcomes should be implemented and reported so groups are treated as equally as possible. In addition, researchers should consider duplicate assessment outcomes to ensure objectivity (Karanicolas et al., 2010 ). Attention to reporting these details will reduce bias, avoid mistaking batch effects for treatment effects, and will improve the transparency of how the research was conducted.

Many life science disciplines use animal models to test their hypotheses. Few studies provide detailed information regarding housing and husbandry and those reports that contain the information typically do not provide any level of detail that could allow for others to follow similar housing procedures. When using animals, care should be taken to adequately describe the housing and husbandry conditions as these conditions could have profound implications on the experimental results (Prager, Bergstrom, Grunberg, & Johnson, 2011 ). At a minimum, the authors should introduce in the abstract the race, sex, species, cell lines, etc. so that the reader will be aware of the population/sample being studied. However, in the methods section, the authors should carefully describe all animal housing and husbandry procedures. For example, it is normally unclear whether animals were single or group housed, and in most journals, the age and/or weight of the animals are commonly omitted (Florez‐Vargas et al., 2016 ). Other factors that are not commonly reported include information on how the animals were transported from a breeder to the experimenter vivarium (see Good practices in the Transportation of Research Animals, 2006), vivarium temperature, humidity, day/night schedules, how often cages are cleaned, how often animals are handled, whether enrichment is provided in a cage, and cage sizes (Prager et al., 2011 ). Requiring a full description of housing and husbandry procedures will be essential to the rigor and transparency of the published studies and could help determine why some studies are not reproducible.

Sex/gender plays an influential role in experimental outcomes. A common practice within research is that findings in one sex (usually males) are generalized to the other sex (usually females). Yet, research consistently demonstrates that sex differences are present across disciplines. For example, as evidence reveals in a recent issue of JNR (see Sex Influences on Nervous System Function ), sex not only matters at the macroscopic level, where male and female brains have been found to differ in connectivity (Ingalhalikar et al., 2014 ), but at the microscopic level too (Jazin & Cahill, 2010 ). The National Institutes of Health as well as a number of funding agencies mandates the inclusion of sex as a biological variable, yet this mandate is not enforced by most journals. Starting at the study design, the authors must review whether the extant literature suggests that sex differences might be observed in the study, and if so, then design and power the study to test for sex differences. Otherwise, the rigor of the study could be compromised. When publishing the results, the authors must account for sex as a biological variable, whenever possible. At a minimum, the authors should state the sex of the subjects studied in the title and/or abstract of the manuscript. The rationale for choosing only one sex if a single sex study is conducted should also be provided, though discussed as a limitation to the generalizability of the findings. Investigators must also justify excluding either males or females. The assumptions that females are more variable than males or that females must be tested across the estrous cycle are not appropriate as these are not major sources of variability (Beery, 2018 ). This policy is not a mandate to specifically investigate sex differences, but requires investigators to consider sex from the design of the research question through reporting the results (Clayton, 2016, 2018 ). In some instances, sex might not influence the outcomes (e.g., Fritz, Amrein, & Wolfer, 2017 ; Segarra, Modamio, Fernandez, & Marino, 2017 ), but balancing sex in animal and cellular models will distinctly inform the various levels of research (Clayton, 2016 ). More specific guidelines for applying the policy of considering sex as a biological variable are also available (Clayton, 2018 ; McCarthy, Woolley, & Arnold, 2017 ), but shifting the experimental group composition should be done in the context of appropriate a priori power analyses. One concern is that sample sizes need to be doubled to identify effects using both female and male subjects, but factorial designs can evaluate the main effects of the treatment and subject sex without increasing the sample size (Collins, Dziak, Kigler, & Trall, 2014 ). While the risk of false‐positive errors associated with testing sex differences in this way is present, reporting that these differences may or may not be present is imperative to understanding how sex influences the function of the nervous system. This practice should be extended to all scientific journals using animal/human subjects.

3.5 Transparent account of the experimental design and statistical approaches

A transparent experimental design, meaning how the experiment is planned to meet the specified objectives, describes all the factors that are to be tested in an experiment, including the order of testing and the experimental conditions. As studies become more complex and interconnected, planning the experimental procedures prior to the onset of experiments becomes essential. Yet even when the experiments are planned prior to their initiation, the experimental designs are often poorly described and rarely account for alterations in procedures that were used in the study under consideration. To provide a more transparent and rigorous approach to describing the experimental design, a new section should be placed after the “subjects” paragraph describing, in detail, the experimental design and deviations made from the original design.

The experimental design section should consist of two main components: (a) a list of the experimental procedures that were used to conduct the study, including the sequence and timing of manipulation; and (b) an open discussion of any deviations made from the original design. The description should include an explanation of the question(s) being tested, whether this is a parameter estimation, model comparison, exploratory study, etc., the dependent and independent variables, replicates (how often the experiments were performed and how the data were nested) and the type of design considered (e.g., completely randomized design, randomized complete block design, and factorial design; see Lin, Zhu, & Su, 2015; Suresh, 2011) for definitions and procedures to implement these designs). Assuming the authors planned the analysis prior to data collection, the authors should describe the specific a priori consideration of the statistical methods and planned comparisons (Weissgerber, Garovic, Winham et al., 2016) or report that no a priori statistical planning was carried out. If the statistical approach deviated from how it was originally designed (see, for example, Registered Reports below), the authors should also report the justification for this change. This open description could help to improve independent research reproducibility efforts and assist reviewers and readers in understanding the rationale for specific approaches.

A precise description of how methodological tools and procedures are prepared and used should also be provided in the experimental design section. Oftentimes, methodological procedures are truncated, forcing the authors to omit critical steps. Alternatively, the authors may report that the methods were previously described but might have modified those procedures without reporting those changes. Due to current publishing constraints, various caveats that go into the methodological descriptions remain unknown. However, this can be remedied easily by journals requiring a full description or step‐by‐step procedure of the experimental protocol used to test the dependent variables. Two options are available for publishing full protocols. First, the protocol could be published in the manuscript, with the reviewers verifying that the procedures are appropriately followed; second, a truncated version of the methods could be published in the manuscript, but the extended methods must be required as supplemental material (the extended methods will be peer reviewed during the submission process). An alternative approach is to deposit step‐by‐step protocols into a database or a data repository such as Dryad, FigShare, or with the Center for Open Science, where they will receive a DOI and can be linked back to the original research article, which will contain the truncated procedures.

3.5.1 Materials Rigorous descriptions of the experimental protocols not only require a level of detail in the description of the experimental design, but also a full account of the resources and how they were prepared and used. A contributing factor to irreproducibility is the poor or inaccurate description of materials. In order for researchers to replicate and build upon published research findings, they must have confidence in knowing that materials specified in a publication can be correctly identified so that they might obtain the same materials and/or find out more about those materials. Most studies do not include sufficient detail to uniquely identify key research resources, including model organisms, cell lines, and antibodies, to name a few (Vasilevsky et al., 2013). While most author guidelines request that the authors provide the company name, city in which the company is located, and the catalog number of the material, (a) many authors do not include this information; (b) the particular product may no longer be available; or (c) the catalog number or lot number is reported incorrectly, thus rendering the materials unattainable. A new system is laying the foundation to report research resources with a unique identification number that can be deposited in a database for quick access. The Resource Identification Initiative standardizes the materials necessary to conduct research by assigning research resource identifiers (RRIDs). To make it as simple as possible to obtain RRIDs, a platform was developed (www.scicrunch.org/resources) to aggregate data about antibodies, cell lines, model organisms, and software into a community database that is automatically updated on a weekly basis and provides the most recent articles that contain RRIDs (Bandrowski et al., 2016). While SciCrunch is among the founding platforms, these identifiers can also be found on other sites, including antibodyregistry.org, benchsci.com, and others. Similarly, though more involved, PubChem offers identification for various compounds such as agonists and antagonists. Simply find the chemical abstract service (CAS) number from the chemical safety data sheet (SDS), input that number into PubChem, and receive the PubChem Chemical Identifier (CID). RRIDs have been successfully implemented in many titles throughout Wiley and are also in use by Cell Press and a number of other publishers. The authors should provide RRIDs and CIDs when describing resources such as antibodies, software (including statistical software used, as this is rarely reported), and model organisms, or compounds used, allowing for easy verification by peer reviewers and experimenters.

3.5.2 Statistical rigor and transparency With most statistical software having a user‐friendly interface, students quickly learn how to perform basic statistical tests. However, users all too often choose inadequate and incorrect statistical methods or approaches or cannot reproduce their analyses since they have only a rudimentary understanding to each test and when to use them (Baker et al., 2014; Lazic, 2010; Strasak, Zaman, Marinell, Pfeiffer, & Ulmer, 2007; Weissgerber, Garovic, Milin‐Lazovic et al., 2016). What's more, the authors do not appropriately describe their statistical approaches in text, partially because tests are performed only after the study is executed. In designing and reporting the experiments, the authors should report normalization procedures, tests for assumptions, exclusion criteria, and why statistical approaches might differ from what the authors originally proposed, if they developed these approaches prior to the onset of data collection. In addition, the authors must also include the statistical software and specific version thereof, descriptive statistics, and a full account of the statistical outputs in the results section. Errors in statistical outputs often arise when the authors (a) do not conduct and report a power calculation (Strasak et al., 2007) or do not distinguish between exploratory and confirmatory analyses (Kimmelman, Mogil, & Dirnagl, 2014); (b) fail to state which statistical tests are used or provide adequate detail about the tests, including the descriptive statistics and a full account of the statistical output; (c) fail to state whether assumptions were examined (Weissgerber et al., 2015); or (d) fail to describe how replicates were analyzed (Lazic, 2010). Moreover, it might be difficult to reproduce statistical output when the authors do not report the statistical software and specific version thereof, fail to include in the manuscript the exclusion criteria or code used to generate analyses, or explain how modifications to the experimental design might lead to changes in how statistical analyses are approached (e.g., independent vs. non‐independent groups) (additional details about these common mistakes can be found in (Weissgerber, Garovic, Milin‐Lazovic et al., 2016; Weissgerber, Garovic, Winham et al., 2016; Weissgerber et al., 2017), but it is important to emphasize that failure to report these variables can lead to errors in data interpretation. 2014 2017 2016 2011 Power analysis calculations or sample size justification for exploratory research, including accuracy in parameter estimation (Maxwell, Kelley, & Rausch, 2008

Statement of the factors tested, types of analyses, and what post hoc comparisons were made

Statement of the statistical tests used and details as to why those tests were chosen, including how the authors choose between parametric or nonparametric tests (assumptions aside)1

Statement of an assessment of assumptions

Statement of how replicates were analyzed (e.g., are western blots performed in duplicate and band pixels averaged?)

Data point exclusion criteria

Statement of how outliers were determined and how they were handled

Descriptions of raw data, including transformation procedures

Within the results, a full account of the test statistic, and where applicable the degrees of freedom, p‐values reported to a consistent number of decimal places (usually three), and statement of whether the test was one‐ or two‐sided Choosing the correct statistical analyses first depends on an appropriate experimental design and mode of investigation (exploratory vs. confirmatory; Kimmelman et al.,). One must decide whether experimental conditions are independent, meaning that no subjects or specimens are related to each other (Weissgerber et al.,; Weissgerber, Garovic, Winham et al.,), whether the conditions are non‐independent or paired, and whether there are any associations between variables (Nayak & Hazra,). The second step is that statistical analyses must include specific details about the test statistics, rationale for choosing each test, a description of whether normal distribution parameters are obtained and a statement about which p‐value level is deemed statistically significant. In addition, a transparent and rigorous statistical analysis section must include the following:

3.5.3 Power analysis Many studies are rejected for publication because of criticism that a study is underpowered, though many more studies are published despite this (Button et al., 2013). Reporting how a sample size was predetermined based on power analyses conducted during the experimental design stage is a good way to avoid this criticism. Researchers are taught to perform these analyses prior to the start of their experiments, but evidence suggests that researchers and peer reviewers do not fully understand the concept of statistical power, have not been given adequate education about the concept, or do not consider the measurement important in designing the experiments (Onwuegbuzie & Leech, 2004). Reviewers and journal editors are beginning to ask authors to address the question of what the power of the study was to detect the observed effect (Goodman & Berlin, 1994; Levine & Ensom, 2001). Determining whether a study is appropriately powered a priori or post hoc is a matter of debate (Levine & Ensom, 2001). Many argue that post hoc power analyses are inappropriate, especially for nonsignificant findings, while others argue that post hoc power analyses are appropriate since a priori power analyses do not represent the power of the ensuring effect, but rather the hypothesized effect (Onwuegbuzie & Leech, 2004). The a priori power analysis is the most common way of determining the sample size for simple experiments and can be easily computed using freely available software such as G*Power. The sample size depends on a mathematical relationship among the (a) effect size of interest; (b) standard deviation (SD); (c) chosen significance level; (d) chosen power; and (e) alternative hypothesis (Festing & Altman, 2002). Yet, as more parameters come into play (for example, within mixed effects modeling), power analysis software becomes more complex (see Power Analysis for Mixed Effect Models in R). Conducting these analyses allows researchers to confidently select a sample size large enough to lead to a rejection of the null hypothesis for a given effect size (Onwuegbuzie & Leech, 2004). However, one limitation to a priori power analyses is that effect sizes and SDs may not be known prior to the research being conducted and may lead to observed effects that are smaller or larger than the hypothesized effects (Wilkinson & Inference, 1999; see also Nuzzo, 2014). Alternatively, if it is conventional to use a specific number of subjects for a particular test, then one can report the calculated effect size for that particular sample size and decide whether more samples would be warranted. Either way, power and sample size calculations provide a single estimate, ignoring variability and uncertainty as such simulations are highly encouraged (see Lazic, 2016). An alternative to the a priori power analysis is a post hoc power analysis (SPSS calls this “observed power”) or confidence intervals. The post hoc power analysis takes the observed effect size as the assumed population effect, though this computation might be different from a true population effect size, which might culminate in a misleading evaluation of power (Onwuegbuzie & Leech, 2004). Post hoc power analyses always show there is low power with respect to nonsignificant findings (Levine & Ensom, 2001). Thus, utilizing the post hoc power analysis must be done with extreme care and should never be a substitute for the a priori power analysis. In fact, many in the statistical community see post hoc analyses as a waste of effort and recommend abandoning this approach (Hoenig & Heisey, 2001); see also https://dirnagl.com/2014/07/14/why-post-hoc-power-calculation-does-not-help/and https://daniellakens.blogspot.com/2014/12/observed-power-and-what-to-do-if-your.html). If a reviewer or journal requests a power analysis, we recommend that rather than using post hoc power analyses, report confidence intervals to estimate the magnitude of effects that are consistent with the statistical data reported (Goodman & Berlin, 1994; Levine & Ensom, 2001; Smith & Bates, 1992). Alternatively, if increasing power is a necessity and/or sample sizes are already at their limits for financial or logistic reasons, one should consider alternative approaches, which are well described by Lazic; these include: (a) using fewer factor values for continuous predictors; (b) having a more focused and specific hypothesis test; (c) not dichotomizing or binning continuous variables; (d) using a crossed or factorial design rather than a nested arrangement (Lazic, 2018). We also advise authors to determine whether a parametric or nonparametric test is the most appropriate for the obtained data. Analogues to ordinary parametric tests (e.g., t‐test or ANOVA, etc.) can be performed even if data are skewed or have nonnormal distributions; multiple robust analytics are available for these circumstances (see Wilcox, 2013) as long as the sample size is sufficient. Importantly, parametric tests also generally have somewhat more statistical power than nonparametric tests and are more likely to detect a significant effect if one exists. Alternatively, when one's data are better represented by the median, nonparametric tests may be more appropriate, especially when data are skewed enough that a mean might be strongly affected by the distribution tail, whereas the median estimates the center of the distribution. Nonparametric tests may also be more appropriate when the obtained sample size is small, as occurs in many fields where sample sizes average less than eight per group (Holman et al., 2016) or when the data obtained are ordinal, ranked, or there are outliers that cannot be removed (Frost, 2015). Beware, however, that meaningful nonparametric testing with sample sizes too low (e.g., n < 5) contains very little appreciable power to reveal an effect, if indeed one is present; difficulties due to violations of the underlying statistical assumptions of the particular test being used might be present. Bayesian analyses with small sample sizes are also possible, though estimates are highly sensitive to the specification of the prior distribution.

3.5.4 Graphical representation of data Figures illustrate the most important findings from a study by conveying information about the study design in addition to showing the data and statistical outputs (Weissgerber et al., 2017; Weissgerber, Garovic, Winham et al., 2016). Simplistic representations to visualize the data are commonly used and are often inappropriate. For example, bar graphs are designed for categorical data; when used to display continuous data, bar graphs with error bars omit key information about the data distribution (see also Rousselet, Foxe, & Bolam, 2016). To change standard practices for presenting data, continuous data should be visualized by emphasizing the individual points; dot plots (e.g., univariate scatterplots) are strongly recommended for small samples, along with plots such as violin plots (or overlaid points on the plots) to provide far more informative views of the data distributions when samples are sufficiently large. Bar graphs should be reserved for categorical data only. Moreover, graphic data plots involving multiple groups are often shown as overlaid, but should be “jittered” across the X‐axis so that each discrete data point can be visualized. The use of jittering means that when there are fewer unique combinations of data points than total observations, the totality of the data distribution is not obscured. By adopting these practices, readers will be better able to detect gross violations of the statistical assumptions and determine whether results would be different using alternate strategies (Weissgerber et al., 2015). When plotting data, it is important to also report the variability of the data. Typically, this is expressed as the SD or standard error of the mean (SEM), but it is important to note that SEM does indicate variability (Motulsky, 2014). The SD is calculated as part of an estimate of the variability of the population from which the sample was drawn (Altman & Bland, 2005; Nagele, 2003). The SEM, on the other hand, describes the SD of the sample mean as an estimate of the accuracy of the population mean. In other words, the SD shows how many points within the sample differ from the sample mean, whereas the SEM shows how close the sample mean is to the population mean (Nagele, 2003). The main function of SEM is to help construct confidence intervals, which are a range of values that take into account the true population value (usually an unknown), so that one can quantify the proximity of the experimental mean to the population mean (Barde & Barde, 2012). Yet deriving confidence intervals around one's data (using SD) or the mean (using SEM) is premised on those data being normally distributed. Robust estimators are increasingly important as heteroscedasticity (having subpopulations with differing variabilities) is a frequent consequence of real‐world measurement. Traditional data transformations are an attempt to cope with this phenomenon but for many, such transformations may not actually serve to resolve anything and may add a layer of unnecessary complexity. In determining which estimate of variability to depict graphically, it is important to remember that the SD is used when one wants to know how widely scattered measurements are or the variability within the sample, but if one is interested in the uncertainty around the estimate of the mean measurement or the proximity of the mean to the population mean, SEM is more appropriate (Nagele, 2003). When plotting data variability, it is important to consider that when SEM bars do not overlap, the viewer cannot be sure that the difference between the two means is statistically significant (see Motulsky, 2014). We also note that it is misleading to report SD's in the narrative and tables but plot SEMs. Furthermore, unless an author specifically wants to inform the reader about the precision of the study, SD should be reported as it quantifies variability within the sample (Altman & Bland, 2005; Barde & Barde, 2012; Nagele, 2003). Therefore, the optimal method to visualize data variability is to display the raw data, but if that makes the graph too difficult to read, instead show a box‐whisker plot, frequency distribution, or the mean ±SD (Motulsky, 2014).

3.5.5 Inclusion of statistically significant and nonsignificant data The probability that a scientific research article is published traditionally depends on the novelty or inferred impact of the conclusion, the size of the effect measured, and the statistical confidence in that result (Matosin et al., 2014; Scargle, 2000). The consequence of obtaining negative results can lead to a file‐drawer effect; scientists ignore negative evidence that does not reach significance and intentionally or unintentionally select the subsets of data that show statistical significance as the outcomes of interest (Munafo et al., 2017). This publication bias skews scientific knowledge toward statistically significant or “positive” results, meaning that the results of thousands of experiments that fail to confirm a result are filed away (Scargle, 2000). These data‐contingent analysis decisions, also known as p‐hacking (Simmons, Nelson, & Simonsohn, 2011), can inflate spurious findings and lead to misestimates that might have consequences for public health. To combat the stigma of reporting negative results, we encourage authors to provide a full account of the experiment, to explicitly state both statistically significant and nonsignificant results, and to publish papers that have been rigorously designed and conducted, irrespective of their statistical outcomes. In addition, some organizations such as the European College of Neuropsychopharmacology are offering prizes in neuroscience research to encourage publication of data where the results do not confirm the expected outcome or original hypothesis (see ECNP Preclinical Network Data Prize). Published reports of both significant and nonsignificant findings will result in better scientific communication among and between colleagues.

3.5.6 Real and perceived conflicts of interest Though objectivity of a researcher or group is assumed, conflicts of interest may exist and could be a potential source of bias. Conflicts of interest largely focus on financial conflicts (Als‐Nielsen, Chen, Gluud, & Kjaergard, 2003; Thompson, 1993), but they can also occur when an individual's personal interests are in conflict with professional obligations, including industrial relationships (Young, 2009). Conflicts, whether real or perceived, arise when one recognizes an interest as influencing an author's objectivity. This can occur when an author owns a patent, or has stock ownership, or is a member of a company, for example. All participants in a paper must disclose all relationships that could be viewed as presenting a real or perceived conflict of interest. When considering whether a conflict is present, one should ask whether a reasonable reader could feel misled or deceived. While beyond the scope of this article, the Committee on Publication Ethics offers a number of resources on conflicts of interest.