On the Bias and Stability of the Results of Comparative Judgment

Introduction

Comparative judgment is a method that allows measurement of a competence by comparison of items. When items are compared in pairs, comparative judgment is also known as pairwise comparison. This method has been used in different contexts ranging from sports to marketing to educational assessment, with different models for each context (e.g., Agresti, 1992; Böckenholt, 2001; Maydeu-Olivares, 2002; Maydeu-Olivares and Böckenholt, 2005; Böckenholt 2006; Stark and Chernyshenko, 2011; Cattelan, 2012; Brinkhuis, 2014). In educational measurement, where comparative judgment is becoming an increasingly popular assessment method (Lesterhuis et al., 2017; Bramley and Vitello, 2018), items are mostly students’ responses to an assignment or an examination. The assignment or the examination is used to measure a competence of the students, and the students’ responses give an indication of their competence level. The method has been used in a variety of contexts, ranging from art assignments (Newhouse, 2014) to academic writing (Van Daal et al., 2016) and mathematical problem solving (Jones & Alcock, 2013). These contexts have in common that the competencies are difficult to disentangle into sub-aspects together defining the competencies. Therefore, they are difficult to measure validly using analytical scoring schemes such as rubrics or criteria lists (Van Daal et al., 2016), which are conventional measurement methods used in education. In contrast to these analytic measurement methods, which assume that a competence can be operationalized by means of a list of sub-aspects and evaluate each aspect separately, comparative judgment is a holistic measurement method where a competence is evaluated as a whole (Pollitt, 2012); simply asking which of two items scores higher on the competence of interest suffices.

For complex competencies like art assignments, academic writing, and mathematical problem solving, it is possible that a higher validity can be obtained using comparative judgment instead of rubrics or criteria lists (Pollitt, 2012; Van Daal et al., 2016) because of its holistic character and the greater possibility of raters to use their expertise in their judgments compared to rubrics or criteria lists. In addition to the claim of higher validity of comparative judgment, Pollitt (2012) claimed that comparative judgment also results in higher reliability compared to using rubrics or criteria lists. However, later research has shown that this claim is likely to be too optimistic for the reported numbers of comparisons per item (e.g., Bramley, 2015; Bramley and Vitello, 2018; Crompvoets et al., 2020; Crompvoets et al., 2021), and that the extent to which high reliability that can be obtained using comparative judgment is limited (Verhavert et al., 2019).

To explain why Pollitt’s (2012) claim is too optimistic, we first define two types of reliability in the context of comparative judgment: the benchmark reliability (Crompvoets et al., 2020, 2021) and the Scale Separation Reliability (SSR; e.g., Bramley, 2015; Crompvoets et al., 2020). Both forms of reliability are based on parameters of the Bradley-Terry-Luce (BTL; Bradley and Terry, 1952; Luce, 1959) model. This model is defined as follows. Let $K$ be the number of items, let $i$ and $j$ ($i,j=1,\dots ,K$) be item indices, and let ${\text{θ}}_i$ and ${\text{θ}}_j$ be the parameters of items i and j. Furthermore, let $X_{ij}$ be the outcome of the inter-item comparison where $X_{ij}=1$ means that item $i$ was preferred to item $j$, and $X_{ij}=0$ means that item $j$ was preferred to item $i$. The BTL model defines the probability that item i is preferred to item j in a paired comparison by means of

$P\left(X_{ij}=1{\text{|θ}}_i,{\text{θ}}_j\right)=\frac{\text{exp}\left({\text{θ}}_i-{\text{θ}}_j\right)}{1+\text{exp}\left({\text{θ}}_i-{\text{θ}}_j\right)}.(1)$

We interpret $\text{θ}$ as an item parameter, but we may also interpret it as a person parameter for the competence of one person. For example, $\text{θ}$ may represent the quality of a student’s work, which in turn represents the competence level of the student. Thus, items and persons are not clearly distinguished in the BTL model for comparative judgment.

The benchmark reliability is only known in simulated data and is computed as the squared correlation between the true (simulated) item parameters and the item parameter estimates. Let $\text{θ}$ be the item parameter in the generating model and let $\widehat{\text{θ}}$ be the item parameter estimate. The benchmark reliability can then be computed as

${\rho }_{\widehat{\text{θ}}\widehat{\text{θ}}\prime }=\text{cor}{(\text{θ},\widehat{\text{θ}})}^2.(2)$

This definition of reliability corresponds with the definition of reliability as ${\text{ρ}}^2\left(\text{θ},\widehat{\text{θ}}\right)$ in classical test theory (Lord and Novick, 1968), where $\text{θ}$ represents the true score and $\widehat{\text{θ}}$ represents the observable test score. Since we are interested in reliability of the measurement of a specific set of items, benchmark reliability is used as the true reliability of this set of items.

The SSR is an estimate of reliability that is based on the Index of Subject Separation formulated by Andrich and Douglas (1977, as cited in Gustafsson, 1977) and is computed as follows. We assume that items are compared in pairs and that the location parameters of these items on the latent competence scale are of interest. Let $S^2\left(\text{θ}\right)$ be the estimated true variance of the object parameters and let $S^2\left(\widehat{\text{θ}}\right)$ be the variance of the estimated object parameters. Furthermore, let $MSE$ be the mean of the squared standard errors corresponding to the item parameter estimates, computed as

$MSE= \frac{1}{K}{\displaystyle \sum }_i^{K}SE{({\widehat{\text{θ}}}_i)}^2.$

The SSR can then be written as

$SSR=\frac{S^2\left(\text{θ}\right)}{S^2(\widehat{\text{θ}})}(3)$

where

$S^2\left(\text{θ}\right)=S^2(\widehat{\text{θ}})-MSE,$

that is, the observed variance minus an error term (Bramley, 2015).

Research (Bramley, 2015; Bramley and Vitello, 2018; Crompvoets et al., 2020) has shown that the SSR might overestimate reliability (Eq. 2) in certain situations. These include the use of certain adaptive algorithms to select the pairs that raters have to compare. Pollitt’s (2012) claim that comparative judgment results in higher reliability than using rubrics or criteria lists is based on a study using an adaptive algorithm to select the pairs that are compared in combination with the SSR. Other situations in which the SSR may overestimate benchmark reliability are when raters behave inconsistent amongst each other, which would be reflected in the BTL model by different parameters for the same items, and perhaps when the true variance of the item parameters is below 1 as well (Crompvoets et al., 2021). The result that the SSR may overestimate reliability suggests why Pollitt’s (2012) claim that comparative judgment results in higher reliability is likely too optimistic. Moreover, the result that the SSR may overestimate reliability is problematic because 1) reliability estimates should provide a lower bound to reliability to avoid reporting reliability that is too high and therefore promises too much (Sijtsma, 2009; Hunt and Bentler, 2015) and 2) most recommendations about the number of required comparisons are based on achieving at least a user-defined value of the SSR (e.g., Verhavert et al., 2019).

To the best of our knowledge, no one has thoroughly investigated and reported the positive bias of the SSR. Previous research that reported the bias of the SSR has stopped at the conclusion that the SSR was biased (Bramley, 2015; Bramley and Vitello, 2018) or has only led to speculations about the meaning of the bias due to either adaptive pair selection (Crompvoets et al., 2020), different rater probabilities, or small true variances (Crompvoets et al., 2021).

One might reason that the behavior of the SSR needs no investigation, because its value can easily be derived from the two components $S^2\left(\widehat{\text{θ}}\right)$ and $MSE$ (Eq. 3). The strategy to vary only one component and keep the other components constant shows how the value of the measure changes with the value of the component. However, both components of the SSR, $S^2\left(\widehat{\text{θ}}\right)$ and $MSE$, are based on the parameter estimates $\widehat{\theta }$ from the underlying model. This means that a shift in the item parameters affects both components simultaneously, which renders the strategy unrealistic for investigation of the SSR. In addition, all item parameter estimates are mutually dependent because we estimate the parameters based on comparisons of the items with each other. This means that every additional comparison changes all item parameter estimates, so we cannot vary one item parameter estimate keeping the other item parameter estimates constant. Moreover, the changes of item parameter estimates after one comparison depend on the parameters of the items that are compared; the outcome of the comparison, which is not always straightforward because we use a probabilistic model; the total number of items and their parameters; and the outcomes of all previous comparisons, which is not always straightforward due to the use of a probabilistic (e.g., BTL) model. In conclusion, instead of influencing the components of the SSR directly, we can only influence the set of item parameters, which influences the comparison data, which influences the parameter estimates, which influences the components of the SSR. Therefore, it is highly relevant to investigate the behavior of the SSR.

Because all quantities needed to estimate the SSR (Eq. 3) are based on the parameter estimates $\widehat{\theta }$ from the underlying model, this study focused on the parameter estimates used in the computation of the SSR. Specifically, we investigated the bias and stability of the parameter estimates. We define these outcomes in the Method section. Because parameter estimates depend on the amount of data available, we investigated bias and stability of the parameter estimates in relation to the number of comparisons.

The goal of this study was to gain insight into the bias and stability of the parameter estimates and the SSR of comparative judgment in educational measurement from two perspectives. In addition, we aimed to use this information either to support the guideline about the number of required comparisons per item from Verhavert et al. (2019) or to provide a new guideline based on the results from this study. First, we adapted the guideline for the required number of observations to obtain stable results for the one-parameter item response model or Rasch model (Rasch, 1960) for regular multiple choice tests to the BTL model used for comparative judgment. Second, we investigated the bias and stability of the parameter estimates and SSR of comparative judgment in a simulation study. In the discussion, we will reflect on the two perspectives.

Sample Size Guideline Adaptation to the Bradley-Terry-Luce Model

To determine the required number of observations to obtain stable model parameters, most researchers and test institutions use experience as their guide. One reason for this may be that the literature about sample size requirements to obtain stable model parameters is sparse and seems limited to conference presentations (Parshall et al., 1998), articles that were not subjected to peer review (Linacre, 1994), a framework used to assess test quality written in a non-universal language (Evers et al., 2009), or a brief mention in a book (Wright and Stone, 1979, p. 136). Parshall et al. (1998) and Evers et al. (2009) describe the guideline that for the one-parameter item response model, at least 200 observations per item are required to obtain stable item location parameter estimates. Wright and Stone (1979) suggest using 200 observations for test linking using the Rasch model, although they, and Linacre (1994), also mention that fewer observations may be sufficient to obtain sufficiently stable parameter estimates for some purposes. When the model parameters are considered sufficiently stable depends on the context. Because we encountered the guideline of 200 observations per item for several purposes and it is used often in practice, we used this guideline as a starting point.

The literature about guidelines for the Rasch model may be sparse, but for the mathematically related (Andrich, 1978) BTL model, no guidelines exist that describe how many observations are required in educational measurement for obtaining stable item parameter estimates. In this section, we first describe how the Rasch model and the BTL model are related, and then adapt the guideline from the Rasch model to the BTL model. In the Discussion section, we will evaluate this guideline in relation to the outcomes of the simulation study from the next section and in relation to the literature.

The Rasch model is defined as follows. Let $N$ be the number of persons in the sample, let $i$ ($i=1,\dots ,N$) be the person index, and let ${\text{θ}}_i^{\text{∗}}$ be the parameter of person $i$ on the latent variable scale, where the ∗ indicates that ${\text{θ}}_i^{\text{∗}}$ differs from ${\text{θ}}_i$ used in the BTL model (Eq. 1). Let $K$ be the number of items, let $j$ ($j=1,\dots ,K$) be the item index, and let ${\text{β}}_j$ be the parameter of item $j$ on the latent variable scale. Furthermore, let $X_{ij}$ be the outcome of the person-item comparison where $X_{ij}=1$ means that person $i$ answered item $j$ correctly, and $X_{ij}=0$ means that person $i$ answered item $j$ incorrectly. The Rasch model defines the probability that person i answers item j correctly by means of

$P\left(X_{ij}=1{\text{|θ}}_i^{\text{∗}},{\text{β}}_j\right)=\frac{\text{exp}\left({\text{θ}}_i^{\text{∗}}-{\text{β}}_j\right)}{1+\text{exp}\left({\text{θ}}_i^{\text{∗}}-{\text{β}}_j\right)}.(4)$

We note that although mathematically it would have made sense to use ${\text{β}}_i$ and ${\text{β}}_j$ in the formulation of the BTL model (Eq. 1) for equivalence with the Rasch model, we chose to follow the conventional notation of the BTL model in comparative judgment contexts using $\text{θ}$ notation for the items.

Even though the Rasch model and the BTL model have different parametrization (Verhavert et al., 2018), Andrich (1978) showed that the equations for the Rasch model and the BTL model are equivalent. This means that a person-item comparison in the Rasch model is mathematically equivalent to an inter-item comparison in the BTL model. Therefore, it makes sense to adapt the guideline for the Rasch model about the required number of observations for stable model estimates to the BTL model.

Our starting point for the guideline adaptation is the item, since items are present in both the Rasch model and the BTL model. In addition, the guideline Parshall et al. (1998) suggested aims at obtaining stable item parameter estimates. We assume that the number of items in the test that the Rasch model analyzes is the same as the number of items in the set of paired comparisons that is analyzed by means of the BTL model. However, the manner in which we obtain additional observations for an item differs between the models. Each observation for an item in the Rasch model is obtained from a person belonging to a population with many possible parameter values, whereas each observation for an item in the BTL model is obtained from an item in the fixed set of items under investigation. Therefore, for the BTL model, the information obtained from one observation may depend on the item parameters in the set, which is different for the Rasch model, where the information also depends on the sample of persons.

There are two ways to adapt the guideline from the Rasch model for use with the BTL model. The first adaptation is to equate the number of required observations per item for the BTL to the required number for the Rasch model; that is, 200 observations per item (Guideline 1). Since each comparative judgment/observation for the BTL model contains information about two items, this adaptation means that compared to the Rasch model, we need half of the total number of observations. We illustrate this with an example. Suppose we have 20 items in both models. The guideline of 200 observations per item for the Rasch model means that we need $200\left(\text{persons}\right)\times 20\left(\text{items}\right)=\mathrm{4,000}$ observations in total for a 20-item test to obtain stable item parameter estimates. The adapted guideline of 200 observations per item for the BTL model means that we need $200\left(\text{comparisons per item}\right)/2\left(\text{items per comparison}\right)\times 20\left(\text{items}\right)=2000$ observations in total for a 20-item test to obtain stable item parameter estimates.

The second possibility is to equate the total number of observations for a set of items instead of the number of observations of one item. Continuing the example from the previous paragraph, 4,000 observations are required for a set of 20 items for the Rasch model to obtain stable item parameter estimates using Parshall et al.’s (1998) guideline. Adapted to the BTL model following the second guideline (i.e., equating the total number of observations for a set of items), this would mean that 4,000 paired comparisons in total are required to get stable item parameter estimates, which would mean $\left(\mathrm{4,000}\text{ comparisons}\times 2\text{ items per comparison}\right)/20\text{ items }=400$ observations per item. This is our Guideline 2. This means that compared to the Rasch model, we need twice as many observations per item for stable item parameter estimates from the BTL model. This makes sense, because each observation in a comparative judgment setting contains information about two items, so only half of the information concerns each item. We will evaluate both guidelines in the discussion section of this paper. One should note that the current recommendations for the numbers of comparisons per item based on a meta-analysis of comparative judgment applications range from 12 to 37 (Verhavert et al., 2019), which shows a large discrepancy with both the 200 and 400 comparisons per item according to the two adapted guidelines.

For the BTL model, the limited number of unique comparisons implies that the number of items in the set influences which numbers are compared, even though the number of observations per item does not change for different numbers of items. The number of items in the set is nonlinearly related to the number of unique comparisons in a comparative judgment setting. This means that the number of times each unique comparison is made differs for different numbers of comparisons. Table 1 illustrates this: using guideline 2, for 20 items, all unique comparisons should be made 21 times (on average). On the other hand, for 1,000 items, all unique comparisons should be made 0.4 times, which means that not even all unique comparisons are made.

TABLE 1

TABLE 1. Total number of observations and number of complete designs according to the translated guideline for the BTL model for different numbers of items.

Bias and Stability of Scale Separation Reliability Components

We investigated in a simulation study: 1) How many comparisons are required to obtain a stable and unbiased variance of the parameter estimates, $S^2\left(\widehat{\text{θ}}\right)$; 2) how many comparisons are required to obtain a coverage of 95%-confidence intervals for the parameter estimates $\widehat{\theta }$ using the standard errors $\text{SE}\left(\widehat{\theta }\right)$ of 95%; and 3) how the $\text{SSR}$ develops with increasing number of comparisons. We investigated these outcomes in situations in which we expected the SSR to underestimate benchmark reliability, because it is easier to understand the SSR and its components in these situations than in situations where we do not know why the SSR overestimates benchmark reliability. The R-code of the simulation study is available at https://osf.io/x7qzc/.

Methods

Simulation Set-Up

The simulation design had two factors. First, we varied the number of items $N=\{20, 30, 50, 100\}$ to investigate whether the number of items affects the stability of the SSR estimate. Second, we used five different variances of the simulated item parameters. In the first condition, we used a variance of zero, which means that all items had the same location on the scale. We used this condition as a benchmark to investigate when the SSR was stable at zero, because the SSR should be zero if the true variance is zero, see (Eq. 3). In the second condition, we used a variance of 1.59, which is a realistic value based on the argumentative writing dataset ‘having children’ used in Van Daal (2020, data retrieved from https://osf.io/wpbhk/?view_only=7aa609162ca146bbbbe9236c9224b668). Argumentative writing refers to one’s ability to express, argue for, and refute objections of one’s opinion about a specific topic (Van Daal, 2020, p. 175). This dataset contained 1,224 comparative judgments performed by 55 raters of 135 texts written by students in the fifth year of secondary education on the topic ‘having children’. Based on a comparison with the summary of several datasets in the meta-analysis of Verhavert et al. (2019), we argue that this dataset is realistic and representative of datasets obtained using comparative judgment for educational measurement. Furthermore, we added the variance conditions 0.5, 1, and 3 to obtain information about the results in between and beyond the benchmark variance and the realistic variance.

For each of the 4 (Number of Items) x 5 (Variance of Items) = 20 design conditions, we repeated the same procedure 100 times. We first selected to item pairs (1,2) (2,3), (3,4), et cetera, until ($K-1,K$) and ($K$,1) to create a linked comparison design. For each item pair, we simulated a comparison in which the probability of preferring one item to the other was given by the BTL model (Eq. 1). After these $K$ comparisons, we estimated the BTL model using the open-source R-code from Crompvoets et al., 2020. This code uses an Expectation Maximization algorithm based on Hunter (2004) to obtain Maximum Likelihood estimates of the parameters. We used the parameter estimates from the BTL model to compute $S^2\left(\widehat{\text{θ}}\right)$ and the SSR for the first time. Subsequently, we compared a randomly selected pair of items, estimated the BTL model parameters, and computed $S^2\left(\widehat{\text{θ}}\right)$ and the SSR after each comparison until the maximum number of comparisons of 200 per item was reached. Lastly, we computed the number of comparisons per item required to obtain a stable variance of the parameter estimates $S^2\left(\widehat{\text{θ}}\right)$ at the true parameter variance and the number of comparisons per item required to obtain a correct coverage of the 95% confidence interval for the parameter estimates $\widehat{\theta }$.

We determined the number of comparisons per item required for a stable and accurate estimate to be the number of comparisons where $12K$ subsequent comparisons produced a value within a range around the true value, both for $S^2\left(\widehat{\text{θ}}\right)$ and for the coverage of the 95% confidence intervals. The range of accurate values was defined as the range between 1 standard error below the true value and 1 standard error above the true value. We based the $12K$ subsequent comparisons on the guideline of 12 comparisons per item from the meta-analysis of Verhavert et al. (2018).

Results

Figure 1 shows the development of $S^2\left(\widehat{\text{θ}}\right)$ (top row), $MSE$ (middle row), and the SSR (bottom row) with increasing numbers of comparisons per item of each of the 100 simulations per design cell and of the average for all true variance conditions for 50 items. On average, $S^2\left(\widehat{\text{θ}}\right)$ seems to converge to the true variance, but not for every single simulated data set. Comparing the top- and middle rows, we see that there is much more variation in $S^2\left(\widehat{\text{θ}}\right)$ than in $MSE$ across simulations. The variation in development across simulations of both $S^2\left(\widehat{\text{θ}}\right)$ and $MSE$ was larger for larger true variance values. Interestingly, although $S^2\left(\widehat{\text{θ}}\right)$ and $MSE$ are the only components needed to compute the SSR (Eq. 2), the variation in development across simulations of the SSR shows the opposite trend with smaller variation for larger true variance values.

FIGURE 1

FIGURE 1. Development of $S^2\left(\stackrel{⌢}{\mathrm{\theta }}\right)$, $MSE\left[S\left(\stackrel{⌢}{\mathrm{\theta }}\right)\right]$, and the SSR with increasing numbers of comparisons per item of all 100 simulations (black lines) and of the average (red line) for all true variance conditions for 50 items. The x-axis shows the average number of comparisons per item for interpretation purposes, but the data points are per comparison.

Figure 2 shows the development of bias in $S^2\left(\widehat{\text{θ}}\right)$ (top row) and bias in SSR (bottom row) with increasing numbers of comparisons per item averaged across all 100 simulations with 68% confidence intervals for both true variance conditions and all numbers of items. In general, the bias of $S^2\left(\widehat{\text{θ}}\right)$ was smaller for larger numbers of items. We first describe the results for a true variance of 0. The bias of $S^2\left(\widehat{\text{θ}}\right)$ was larger for smaller numbers of items, but differences in $S^2\left(\widehat{\text{θ}}\right)$ among numbers of items almost disappeared after about 30 comparisons per item. For 20 and 30 items, the SSR overestimated benchmark reliability in the beginning of data collection. For 20 items, this overestimation stopped after only a few comparisons, but then underestimated benchmark reliability by about 0.2 units. For 30 items, it took about 25 comparisons per item to stop the SSR from overestimating benchmark reliability. For 50 items, the SSR closely estimated benchmark reliability after only a few comparisons per object. For 100 items, the SSR closely estimated benchmark reliability after about 40 comparisons.

FIGURE 2

FIGURE 2. Development of bias in $S^2\left(\stackrel{⌢}{\mathrm{\theta }}\right)$ and bias in SSR with increasing numbers of comparisons per item averaged across simulations with 68% confidence intervals for all true variance conditions and all numbers of items. Bias in SSR was computed as SSR—benchmark reliability. For $S^2\left(\stackrel{⌢}{\mathrm{\theta }}\right)$, we used $MSE\left[S\left(\stackrel{⌢}{\mathrm{\theta }}\right)\right]$ to create the confidence interval. For the SSR, we used the SD across simulations to create the confidence interval. The x-axis shows the average number of comparisons per item (up to 50 comparisons per item) for interpretation purposes, but the data points are per comparison.

We next describe the results for the other true variances. In general, the differences among the number of items conditions in $S^2\left(\widehat{\text{θ}}\right)$ were larger for larger true variances. For true variances larger than 1, on average, $S^2\left(\widehat{\text{θ}}\right)$ was underestimated for 100 items, while it was overestimated for lower numbers of items and lower true variances. Except for a true variance of 3, fewer comparisons were required to converge to the true variance for larger numbers of items. The SSR closely estimated benchmark reliability often after a few comparisons but almost always with 30 comparisons per item. Furthermore, on average, the SSR seemed to closely estimate benchmark reliability after fewer comparisons for lower numbers of items, which is the opposite trend of convergence compared to $S^2\left(\widehat{\text{θ}}\right)$. However, the differences in SSR among the numbers of items are quite small in general. One difference worth mentioning is that for 20 items and a true variance of 0.5, the SSR was overestimated in the beginning of data collection, which is more like the condition with a true variance of zero.

Table 2 shows the mean number of comparisons per item required for accurate $S^2\left(\widehat{\text{θ}}\right)$ values. In general, fewer comparisons per item are required on average for larger numbers of items, with the exception of 100 items and a true variance of 3. In addition, more comparisons per item are required on average for increasing true variances, with the exception of 100 items and a true variance of 3. The mean number of comparisons per item required for accurate $S^2\left(\widehat{\text{θ}}\right)$ values ranges from 24 comparisons per item (for 100 items and a true variance of 1.59) to 119 comparisons per item (for 20 items and a true variance of 0.5). Furthermore, the large ranges within each condition indicate that there is a large variation in the number of comparisons per item required across simulations.

TABLE 2

TABLE 2. Mean number of comparisons per item required for accurate estimation of the true variance.

Figure 3 shows the development of the coverage of the 95% confidence intervals for the parameter estimates $\widehat{\theta }$ with increasing numbers of comparisons per item. In general, with the exception of 100 items and a true variance of 3, the coverage was larger than 95%, which indicates that the standard errors of the parameter estimates were overestimated. However, most values are within the range of accurate values. The number of items required for accurate coverage was lower for larger true variances (Figure 3; Table 3). As Table 3 indicates, in many conditions, the coverage was accurate in 12 comparisons per item or under, and it was accurate for at most 25 comparisons per item.

FIGURE 3

FIGURE 3. Development of the coverage of 95% confidence intervals for parameter estimates $\stackrel{⌢}{\mathbf{\theta }}$ with increasing numbers of comparisons per item for all true variance conditions and all numbers of items.

TABLE 3

TABLE 3. Mean number of comparisons per item required for accurate coverage of 95% CI around parameter estimates.

Because the development of $S^2\left(\widehat{\text{θ}}\right)$ and the coverage with increasing number of comparisons per item was different from the development of the SSR, we decided to provide a guideline based on the SSR itself instead of its components. To this end, we computed the number of comparisons per item required for the SSR to underestimate benchmark reliability within a margin in 95% of the cases. Specifically, we calculated how many comparisons per item were required such that the lower bound of the 95% CI of the SSR was between the benchmark reliability and a margin of 0.10, 0.05, 0.03, and 0.01 below the benchmark reliability for each condition. The results are displayed in Table 4. The number of comparisons per item required for the SSR to closely estimate benchmark reliability depended on the number of items in the set and the true variance of the item parameters, which is in line with the bottom row in Figures 1, 2 displaying the SSR in relation to the number of comparisons per item. The number of comparisons per item ranged from 15 to more than 200. In general, smaller margins led to more comparisons per item required, more items in a set led to approximately the same or fewer comparisons per item required, and larger true variances led to fewer comparisons per item required, except for the combination of 20 items and a true variance of 3.

TABLE 4

TABLE 4. Number of comparisons per item required for the SSR to estimate benchmark reliability between the benchmark reliability value and the benchmark reliability value minus the margin in 95% of the cases.

Discussion

The guideline that 200 observations per item are required for stable parameter estimates using the Rasch model (Parshall et al., 1998) was adapted for the BTL model in two ways. Guideline 1 was obtained using the number of observations per item in the Rasch model, resulting in 200 comparisons per item for the BTL model. Guideline 2 was obtained using the total number of observations in a set of items in the Rasch model, resulting in 400 comparisons per item for the BTL model.

In the simulation study, the results showed that the variation in development across simulations of both the estimated variance and the mean squared standard error were larger for larger true variance values, but the variation in development across simulations of the SSR was smaller for larger true variance values. This is interesting, because the estimated variance and the mean squared standard error are the only components of the SSR. Possibly, the variations in the estimated variance and the mean squared standard error are more aligned for larger true variances such that combining them in the SSR leads to less variation. On average, the variance was accurately estimated after 24 to 119 comparisons per item, although the number of comparisons per item differed greatly among simulations. The coverage of the 95% confidence intervals of the parameter estimates showed that the standard errors of the parameter estimates were accurate after 4 to 25 comparisons per item. The SSR could closely estimate benchmark reliability even when the variance of the parameter estimates was still overestimated. When using margins ranging from 0.10 to 0.01 to determine when the SSR closely estimated benchmark reliability, across conditions, the number of comparisons per item ranged from 15 to more than 200.

When we compare the results from the two perspectives, it seems that Guideline 2 of 400 comparisons per item is too pessimistic and overly demanding. Guideline 1 could be useful since several simulations took 200 or more comparisons per item to get stable variance estimates and it took 200 or more comparisons for the SSR to closely estimate benchmark reliability when the margin was 0.01. However, averaged across samples, the variance was accurately estimated after a maximum of 119 comparisons per item, the standard errors of the parameters and the SSR required even fewer comparisons per item, and in most conditions, the SSR closely estimated benchmark reliability after less than 50 comparisons per item. Therefore, Guideline 2 may be too demanding as well.

The alternative guideline we present here is largely based on Table 4. We recommend that comparative judgment applications require at least 41 comparisons per item based on the following considerations. In general, smaller margins led to more comparisons per item required, more items in a set led to approximately the same or fewer comparisons per item required, and larger true variances led to fewer comparisons per item required. With respect to the margin that determines how much the SSR may underestimate benchmark reliability, we are lenient by choosing the largest margin. We believe that this is justified because the benchmark reliability is usually larger than the SSR, and because Verhavert et al. (2019) indicate that the SSR already has high values with this many comparisons per item. If one prefers a smaller margin, we recommend 72 comparisons per item for a margin of 0.05, 112 comparisons for a margin of 0.03, and more than 200 comparisons for a margin of 0.01. With respect to the true variance of the item parameters, we were quite strict by choosing the largest number of comparisons, which was for a true variance of 0.5. Because one can never know the true variance in practice and because our study showed that accurate variance estimation often required many observations per item, we argue that it is best to play safe, that is, to risk performing more comparisons than required for the desired accuracy rather than risking that you do not achieve the desired accuracy by performing too few comparisons. For example, if the number of comparisons for a comparative judgment application is based on a variance of 1, but in reality the true variance is less than 1, the SSR will not be as close to the benchmark reliability as one may believe. With respect to the number of items, we also argue to be strict and play safe. Therefore, we chose the number of comparisons for 20 items for the general guideline, which requires the most comparisons per item. However, as one does know the number of items in their comparative judgment application, the required number of comparisons can be somewhat adjusted to the number of items in this set. Table 4 provides information about this adjustment, but the researcher must make the call, given that we only investigated four numbers of items.

Our guideline of 41 comparisons per item renders comparative judgment less interesting to use in practice than the guideline of 12 comparisons per item Verhavert et al. (2019) suggested. However, 41 comparisons per item are necessary for accurately determining the reliability of the measurement using the SSR. The SSR may overestimate benchmark reliability in individual samples, even when it underestimates reliability on average, especially when the number of comparisons is small. Based on Table 4, we suggest that after 41 comparisons, the risk of overestimating reliability with the SSR in individual samples is largely reduced.

Our guideline concerns reliability estimation by means of the SSR and not benchmark reliability. This means that using fewer than 41 comparisons may result in sufficient benchmark reliability (Crompvoets et al., 2020; Crompvoets et al., 2021). The problem is that we cannot determine whether this is the case based on the SSR. Therefore, if a different reliability estimate would exist for comparative judgment, the guideline might change. Measures like the root mean squared error (RMSE) may be useful in some instances, since it is related to reliability, only in terms of the original scale. However, the fact that the RMSE is scale dependent also makes it more difficult to interpret and to compare between different measurements. Therefore, a standardized measure of reliability, bound between 0 and 1, would be preferred. This is an interesting topic for future research.

In our simulation designs, we did not use adaptive pair selection algorithms or multiple raters who perceived a different truth, which are the situations in previous research where the SSR systematically overestimated benchmark reliability. The results of our study provide a baseline how the SSR and the components used to compute the SSR develop with increasing numbers of comparisons when the SSR is expected to underestimate reliability, as it should. Future research could build on our results by investigating how the components of the SSR develop with increasing numbers of comparisons in situations where the SSR might overestimate reliability. The fact that the SSR might overestimate reliability in some situations is even more reason to use a guideline that reduces the risk of overestimation due to sampling fluctuations.

Our study focused on the components of the SSR because we expected that this would show the cause of the inflation of the SSR. However, our simulation study showed that the estimated variance and standard errors of the item parameters developed differently from the SSR with increasing numbers of comparisons with respect to variation between samples, which is not what we expected. Since the components of the SSR developed differently from the SSR, they do not seem to be the cause of the inflation of the SSR. Future research could also aim at developing alternative reliability estimates to the SSR.

In conclusion, the SSR may overestimate reliability in certain situations, but it can function correctly as an underestimate of reliability even when the variance of the items is overestimated. The SSR can be used when the pairs to be compared are selected without an adaptive algorithm, when raters use the same underlying model/truth, and when the true item variance is at least 1. The variance of the items is likely to be overestimated when fewer than 24 comparisons per item were performed. An adaptation of the guideline for the Rasch model was too pessimistic. We provided a new guideline of 41 comparisons per item, with nuances concerning the number of items and the margin of accuracy for SSR estimation. Future research is needed to further investigate the SSR estimation and to develop an alternative reliability estimate.

Data Availability Statement

The datasets presented in this study can be found in online repositories. The names of the repository/repositories and accession number(s) can be found below: https://osf.io/x7qzc/.

Author Contributions

EC executed the research and wrote the manuscript. AB and KS contributed to the analysis plan and writing of the manuscript.

Conflict of Interest

EC was employed by the company Cito.

The remaining authors declare that the research was conducted in the absence of any commercial or financial relationships that could be construed as a potential conflict of interest.

Publisher’s Note

All claims expressed in this article are solely those of the authors and do not necessarily represent those of their affiliated organizations, or those of the publisher, the editors and the reviewers. Any product that may be evaluated in this article, or claim that may be made by its manufacturer, is not guaranteed or endorsed by the publisher.

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