1 Introduction

Algorithmic pricing (AP) has diffused rapidly across retail markets, with a substantial share of online retailers now relying on pricing algorithms to monitor competitors or automatically adjust prices in real time (Chen et al. 2016; European Commission (DG Competition) 2016; Lindgren et al. 2025; Norwegian Competition Authority 2021). Despite this rapid adoption, we know surprisingly little about whether AP actually improves firm performance.

Much of the existing debate has focused on competition-law concerns. Early discussions emphasized the potential for algorithms to facilitate tacit collusion (Calvano, Calzolari, Denicolò, and Pastorello 2020; Calvano, Calzolari, Denicolò, and Harrington Jr 2020; Harrington Jr 2018). Empirical studies have since documented ambiguous effects: higher observed prices in markets with algorithmic retailers (Assad et al. 2024; Hanspach et al. 2024; Musolff 2022), but little direct proof of coordination. A notable exception, making a stronger argument that at least some AP-retailers are coordinating, can be found in Carling et al. (2025). From a managerial and policy perspective, however, the central question is not only how AP affects market prices, but whether it enhances—or undermines—the financial viability of adopting firms.

This paper addresses that gap. Building on previous work that linked retailer entry into the price comparison website PriceSpy to gains in productivity, profits, and wages (Lindgren et al. 2022), we now turn to the profitability consequences of AP itself. A separate strand of this research program, presented in Lindgren et al. (2025), has already identified which retailers are likely to be algorithmic adopters using detailed product-level data on frequency of price adjustments and market presence. In the present study, we build on the results from Ho et al. (2007) and Iacus et al. (2012a), and focus on outcomes: do algorithmic retailers differ systematically in their profitability, efficiency, and growth compared to otherwise similar non-adopters? To our knowledge, this represents the first cross-country research into how AP adoption by retailers impacts firm-level financial performance.

The motivation is twofold. First, online retail is characterized by intense price competition, yet AP adoption is widespread and growing, including in Nordic markets (Norwegian Competition Authority 2021; Lindgren et al. 2025). Understanding whether algorithmic pricing confers tangible financial advantages is therefore central to explaining its diffusion. Second, international policy debates increasingly treat AP as a double-edged sword: a technology that may sharpen competition and reallocate profits, but whose firm-level effects are poorly understood (Assad et al. 2024; Ezrachi and Stucke 2015). The relevant counterfactual is not simply whether algorithms raise or lower market prices, but whether adopting firms achieve higher returns, margins, or asset efficiency than non-adopters.

Empirically, we compile a harmonized firm-year panel linking PriceSpy coverage, including information regarding AP-adaptation, to financial accounts across seven countries. The data are scaled and converted into a common currency to ensure comparability across sources. Our identification strategy mirrors earlier studies of e-commerce but adapts to the specific setting of time-invariant treatment: each firm is classified as either algorithmic or non-algorithmic throughout the observation window. To address non-random adoption, we employ coarsened exact matching (Blackwell et al. 2009; Iacus et al. 2012a) and related methods and then estimate treatment effects using matched difference-in-differences designs. The focus is squarely on financial outcomes such as profitability, margins, and efficiency, rather than employment.

The remainder of the paper is structured as follows. Section 2 presents the data, including details on harmonization, scaling, currency conversion, and outlier treatment. Section 3 sets out the empirical strategy, Section 4 reports results, and Section 5 discusses implications for profitability, competition, and the diffusion of algorithmic pricing in retail markets.

2 Data

This study builds directly on the identification of algorithmic pricing retailers carried out in Lindgren et al. (2025), in which a classification of retailers as algorithmic or non-algorithmic based on detailed product-level price quote data from the PriceSpy platform, covering seven countries (Denmark, Finland, Norway, Sweden, the United Kingdom, France, and New Zealand) and sixteen product categories. The data collection procedures, the computation of price-change markers, and the heuristic rules for classifying firms are described in full detail in Lindgren et al. (2025). For the purposes of the present analysis, we take the resulting retailer-level classification as given and focus on the consequences of algorithmic pricing for firm performance.

The classification from Lindgren et al. (2025) has been merged with harmonized firm‑year financial accounts to construct a multi‑country panel suitable for comparing the financial outcomes of algorithmic and non‑algorithmic retailers. The panel spans 2010–2024 and includes more than one million firm‑year observations, with coverage varying with the availability and completeness of official filings. Source systems include Eikon, the Swedish House of Finance (SHOF) database, UK Companies House (CH), as well as Pappers (France), Denmark’s Central Business Register (CVR), and Norway’s Brønnøysund Register Centre. Because many filings are not natively machine‑readable, we implement a standardized acquisition workflow: reports are collected from official repositories and vetted aggregators; non‑text documents are processed with language‑aware optical character recognition to recover tabular content; and structured variables are extracted from machine‑readable formats (e.g., XBRL/XML) and from OCR‑derived text using common parsing rules. The unit of observation is the firm‑year, identified by country, company name, and year. While names are not perfect identifiers, this cross‑source linkage is complemented—where available—by platform‑level identifiers for the PriceSpy subset, which provide unambiguous linkage of platform presence, algorithmic status, and financial accounts.

Because the financial data come from multiple providers, a multi-step harmonization was required. Variables were standardized to a common schema; duplicate firm-year entries were resolved by prioritizing Eikon over SHOF; and firm names were normalized through automated mapping and manual checks. Industry and sector codes were consolidated into a new grouping variable to ensure comparability across countries.

A further step ensured consistency in monetary units. SHOF data (reported in thousands of SEK) were scaled by a factor of 1,000, while CH data (reported in millions of GBP) were scaled by 1,000,000. To place all accounts in a common currency, SHOF (SEK) and CH (GBP) values were converted into EUR using ECB year-end exchange rates; Eikon data were already denominated in EUR and required no scaling. This guarantees that balance sheet and income statement items are comparable across sources and countries.

Before analysis, we also undertook targeted data cleaning. Implausible entries such as negative cost of goods sold were corrected, while rows missing key variables (total assets, operating profit, sales) were dropped. In the final stage, residual rows with non-key NA values were removed when they would otherwise bias derived ratios. From the harmonized and cleaned accounts, we constructed measures of firm performance, including return on assets, profit margins, asset efficiency, debt ratios, and inventory dynamics. To reduce the influence of extreme outliers, all measures were winsorized at the 1st and 99th percentiles within each year; sensitivity checks with alternative outlier rules are detailed in Appendix B.

Where official accounts were not readily machine‑readable, we follow a three‑stage retrieval and extraction workflow: (i) annual reports and statutory filings are collected from official repositories and trusted aggregators; (ii) non‑text documents are processed with language‑aware optical character recognition to recover tabular content; and (iii) structured fields are extracted from machine‑readable formats (e.g., XBRL/XML) and from OCR‑derived text using standardized parsing rules. These materials are then consolidated into a unified harmonisation pipeline prior to currency conversion, scaling, and panel‑wide cleaning.

Table 1. Sample Selection and Data Processing Flow
Stage No. of observations
Initial raw data observations 7,095,157
Less: Exclusions after data quality review
• Impossible financial values (negative sales > total assets) 9
• Accounting logic violations 22
• Extreme business outliers (e.g., Fyndiq AB -596% margin) 1
After problematic record removal 7,094,525
Less: Insufficient financial data coverage
• Missing total assets, sales, or operating profit (est. 122,525)
After financial data requirements 6,972,000
Less: Insufficient temporal coverage
• Firms with < 2 years of data (est. 1,472,000)
Final analytical sample 5,500,000
Breakdown by treatment status:
• Algorithmic pricing adopters (identified 2020-2022) ~33 firms
• Non-algorithmic retailers (PriceSpy) ~500 firms
• Other firms (non-retail) ~75000 firms
Download Excel Download Word

Table 1 summarizes the sample selection and data processing flow from raw observations to the final analytical panel, including the breakdown by treatment status. This provides a transparent accounting of inclusion criteria and attrition prior to constructing the country-by-year coverage in Table 2.

Table 2. Sample construction by country, year, and adoption group
Country Group 2010 2011 2012 2013 2014 2015 2016 2017 2018 2019 2020 2021 2022 2023 2024 Total Algo %
Denmark Non-algo 0 1 7 14 14 12 16 17 16 17 14 15 14 14 12 183
Denmark Algo 4 2 4 6 5 7 6 7 6 8 8 8 6 7 7 91 33.2%
Finland Non-algo 0 0 1 5 5 5 5 7 7 7 9 8 9 10 7 85
Finland Algo - - - - - - - - - - - - - - - - 0%
France Non-algo 0 2 7 7 8 10 10 10 11 9 9 10 12 12 12 129
France Algo 0 0 0 0 0 0 0 0 0 1 1 1 1 1 2 7 5.1%
Norway Non-algo 0 2 6 13 19 20 21 23 26 26 31 31 29 29 17 293
Norway Algo 3 2 5 7 6 6 6 6 6 7 8 7 6 6 7 88 23.1%
Sweden Non-algo 194 209 222 226 233 239 251 264 275 292 300 301 303 294 31 3634
Sweden Algo 11 12 13 13 13 14 16 17 17 16 17 20 20 20 2 221 5.7%
UK Non-algo 1 2 3 4 17 23 23 21 17 19 21 23 24 16 12 226
UK Algo 0 0 0 0 2 2 2 4 6 7 7 9 9 8 4 60 21%
Total Non-algo 195 216 246 269 296 309 326 342 352 370 384 388 391 375 91 4550
Total Algo 18 16 22 26 26 29 30 34 35 39 41 45 42 42 22 467 9.3%
Download Excel Download Word

Table 2 provides descriptive statistics on the scope of the harmonized panel by country, distinguishing the number of algorithmic retailers, PriceSpy firms, and total firms with annual report data. These initial counts give a first overview of coverage; a more detailed set of descriptive tables, including coverage rates and adopter/non-adopter comparisons, is provided in Appendix F. These tables show that algorithmic retailers tend to be larger in terms of sales and assets but also display weaker profitability ratios than their non-algorithmic counterparts. These contrasts provide motivation for the subsequent matched analyses, since raw differences may reflect underlying size and sectoral composition rather than the causal effect of algorithmic adoption.

Table 3. Sample Characteristics by Country and Treatment Status
Country Group Firms Obs. ROA Est. ROA [N] Profit Margin Est. Profit Margin [N] Asset Turnover Est. Asset Turnover [N] Log TA Est. Log TA [N] Log Sales Est. Log Sales [N]
Denmark Non-algorithmic 35 183 0.005 (0.423) [183] 0.015 (0.214) [183] 2.905 (1.757) [183] 13.589 (3.269) [183] 14.018 (2.711) [183]
Denmark Algorithmic 14 114 0.131 (0.271) [76] 0.020 (0.008) [12] 4.553 (0.599) [14] 13.897 (2.769) [114] 16.669 (0.000) [14]
Finland Non-algorithmic 10 85 0.035 (0.113) [85] 0.002 (0.065) [85] 3.815 (2.591) [85] 9.603 (1.925) [85] 10.733 (1.749) [85]
Finland Algorithmic 0 0 – – [0] – – [0] – – [0] – – [0] – – [0]
France Non-algorithmic 21 129 0.066 (0.171) [129] -0.035 (0.386) [129] 2.238 (1.049) [129] 9.808 (2.658) [129] 10.278 (2.740) [129]
France Algorithmic 2 7 0.117 (0.031) [7] 0.025 (0.010) [7] 4.916 (0.730) [7] 7.059 (0.221) [7] 8.306 (0.794) [7]
Norway Non-algorithmic 32 293 0.114 (0.162) [293] 0.047 (0.077) [293] 2.801 (1.276) [293] 8.800 (1.710) [293] 9.686 (1.610) [293]
Norway Algorithmic 11 88 0.046 (0.481) [66] 0.059 (0.212) [66] 4.915 (2.944) [87] 13.052 (2.126) [88] 14.454 (1.778) [87]
Sweden Non-algorithmic 503 5015 0.056 (0.212) [5015] -0.004 (0.317) [5015] 2.764 (1.669) [5015] 13.152 (2.266) [5015] 13.822 (2.176) [5015]
Sweden Algorithmic 31 306 0.000 (0.295) [306] -0.069 (0.585) [306] 3.389 (1.640) [306] 12.626 (2.454) [306] 13.545 (2.248) [306]
UK Non-algorithmic 40 226 0.141 (0.270) [226] 0.035 (0.502) [226] 2.484 (1.596) [226] 10.678 (3.032) [226] 11.264 (2.779) [226]
UK Algorithmic 9 60 0.082 (0.264) [53] -0.026 (0.442) [53] 3.370 (1.193) [53] 13.561 (3.250) [60] 14.141 (2.857) [53]
Note: 'Est.' columns show Mean (Standard Deviation), '[N]' columns show [Number of Observations]. Algorithmic = firms using algorithmic pricing; Non-algorithmic = traditional pricing firms.
Download Excel Download Word

Table 3 compares core financial metrics by country and treatment status, reporting mean (standard deviation) and the number of observations. These cross-sectional contrasts complement the coverage counts in Table 2 by showing systematic size and profitability differences that motivate matching.

Table 4. Panel coverage by country
Country Firms Firm-years
Denmark 1273 7602
Finland 3400 22333
France 41186 181918
Norway 6868 51508
Sweden 974666 6757706
UK 14094 73440
Total 1041487 7094507
Download Excel Download Word

Table 4 reports the number of firms and firm-year observations by country in the harmonized panel. The total row clarifies the aggregate scale for subsequent analyses and helps contextualize the sample sizes used in the balance diagnostics (Table 6) and DiD estimates (Table 9).

The resulting dataset is a harmonized, de-duplicated firm-year panel with algorithmic pricing status carried over from Lindgren et al. (2025) and financial outcomes drawn from official accounts. It forms the empirical foundation of the present paper, allowing us to investigate whether algorithmic retailers systematically differ from non-adopters in terms of profitability, efficiency, and growth.

**Figure 1.** Cumulative algorithmic retailers reporting in dataset by year

Figure 1. Cumulative algorithmic retailers reporting in dataset by year

Download figure (Figure 1 - PNG)

Figure 1 documents the staggered reporting of algorithmic retailers in our dataset, with cumulative counts rising unevenly over time. This staggered appearance has two implications for design and interpretation. First, matching: because treated firms enter our observation window at different times, constructing comparable pre-periods requires aligning on consistent pre-treatment windows and ensuring balance on pre-trend covariates for the available histories. Second, the treatment pool: the set of identified adopters grows over time, which can create imbalances if early and late adopters differ systematically (size, sector, geography). Our CEM procedure and TWFE specification address these concerns by (i) matching within country/sector and coarsened bins for size and leverage, and (ii) absorbing time shocks with year fixed effects while restricting comparisons to periods where common support exists.

3 Empirical Strategy

This paper studies the consequences of algorithmic pricing for firm performance using the retailer classifications developed in Lindgren et al. (2025). In that study, retailers were identified as algorithmic or non-algorithmic from PriceSpy product-level price histories. Here we treat that classification as given and time-invariant at the firm level: each firm is either an adopter or a non-adopter throughout the sample. Because the exact adoption dates are not observed, we rely on timing assumptions treating adoption as occurring within a 2016-2020 window.

A central challenge is that firms self-select into adoption: retailers that implement algorithmic pricing may already differ from non-adopters in terms of size, market scope, or financial health. Simply comparing raw profitability would therefore risk conflating adoption effects with pre-existing differences. To address this issue, our research design combines matching methods with regression-based estimators in a way that mimics a randomized experiment.

Matching and sample construction. The first step is to construct a balanced comparison set of adopters and non-adopters based on pre-treatment characteristics. We employ coarsened exact matching (CEM; Blackwell et al. (2009); Iacus et al. (2012a); Iacus et al. (2012b)). A desirable feature of CEM is that improved balance in one covariate does not affect the imbalance of other covariates, since the researcher determines the maximum level of imbalance between treated and control-group firms for each covariate (Iacus et al. 2012a). CEM has also been shown to reduce model dependence, implying that empirical findings will be more robust to estimation model and model specification choices (Iacus et al. 2012a).

Exact matching is imposed on country and sector, while continuous variables such as firm size, profitability, leverage, liquidity, and recent growth are coarsened into quantile bins. Let \(w_i\) denote the resulting CEM weights, where unmatched firms receive \(w_i = 0\). Balance is then evaluated using standardized differences and multivariate imbalance measures.

Our treatment group consists of firms identified as algorithmic pricing adopters based on their presence in the PriceSpy database during 2020-2022, cross-referenced with systematic analysis of pricing behavior patterns. This procedure yields a finite set of treatment firms with sufficient pre- and post-treatment observations for causal identification. In the matched panels used for estimation, the number of treated firms is reported in Table 7 (“Treated firms (matched)”) and varies by outcome depending on data availability and balance constraints. Importantly, matched sample sizes are outcome-contingent because each outcome applies its own non-missing filter before matching; including leverage (DebtRatio) in the match improves balance but typically reduces the matched treated sample by roughly 5–6 retailers due to higher missingness in that covariate. The control group comprises firms matched to treatment units using Coarsened Exact Matching (CEM) on key pre-treatment characteristics that capture the fundamental drivers of firm performance and algorithmic pricing adoption propensity.

The matching strategy employs exact matching on country and sector to control for institutional differences and industry-specific factors that may systematically affect both the likelihood of algorithmic pricing adoption and subsequent firm performance. For continuous variables, we implement coarsened matching on firm size (measured by log total assets and log sales, both winsorized) and capital structure (measured by debt ratio, winsorized) to ensure treatment and control firms are comparable along these critical dimensions. This approach balances the need for precise matching with sufficient sample sizes for reliable statistical inference.

The matching procedure applies CEM separately for each outcome variable to optimize balance while maintaining sufficient sample sizes for reliable inference. Control weights are capped and trimmed to prevent individual control firms from disproportionately influencing treatment effect estimates, ensuring that our results reflect the average treatment effect rather than the influence of particular outlying firms.

Two-stage matching to accommodate staggered histories. Because adopters appear in the data at different times and some lack usable pre-treatment histories, we use a two-stage CEM design: - Pre-history cohort: for treated firms with observations before 2016, we match within the reference pre-year (2015 where available) using exact country/sector and coarsened bins for Log(TA), Log(Sales), Debt Ratio, and—when available—lagged outcome summaries from the pre-period. Matching is year-cohort specific to avoid comparing across macro regimes. - Post-only cohort: for treated firms without pre-2016 data, we match in a single post reference year (preferentially 2020, otherwise the earliest post-2015 year observed) using the same exact and coarsened covariates (without lagged outcomes). Matching is again constrained within the same year cohort.

We then union the matched cohorts and construct firm weights as follows: treated firms receive weight 1; control firm weights are the CEM weights aggregated to firm level (maximum across cohorts), trimmed at the 99th percentile and capped at 5 to limit influence. We keep only firms with support on both sides of the treatment boundary and require each matched firm to contribute at least one pre- and one post-treatment observation to the analytical panel. The target match ratio is up to 5 controls per treated firm within strata. This procedure enforces common support within country/sector-by-year strata while accommodating staggered reporting of adopters.

We assess covariate balance prior to estimation using standardized mean differences (SMD) for the matched panels. Figures 2–4 display balance for the three analysis samples (Profit Margin, ROA, Sales per Total Assets). As a practical benchmark, we treat |SMD| ≤ 0.25 as indicating acceptable balance; values modestly above this threshold can arise in small, coarsened strata and are interpreted as marginal. In our context, matching within country/sector and coarsened bins for firm size and leverage yields balance that is generally at or below this threshold, with any residual imbalances addressed by the inclusion of time-varying controls in the TWFE specification. Summary statistics are reported in Table 5 and standardized-difference diagnostics are summarized in Table 6.

**Figure 2.** Covariate Balance: Profit Margin

Figure 2. Covariate Balance: Profit Margin

Download Balance Plot (PNG)
**Figure 3.** Covariate Balance: ROA

Figure 3. Covariate Balance: ROA

Download Balance Plot (PNG)
**Figure 4.** Covariate Balance: Sales per TA

Figure 4. Covariate Balance: Sales per TA

Download Balance Plot (PNG)

Estimation. With the matched sample in place, we estimate the consequences of algorithmic pricing using difference-in-differences estimation. Our primary empirical specification employs weighted two-way fixed effects difference-in-differences estimation:

\[Y_{it} = \alpha_i + \gamma_t + \beta \cdot Post_{it} \times Treat_i + \mathbf{X}_{it}'\delta + \epsilon_{it} \tag{1}\]

where \(Y_{it}\) represents the outcome variable for firm \(i\) in year \(t\), \(\alpha_i\) are firm fixed effects that control for time-invariant unobserved heterogeneity, \(\gamma_t\) are year fixed effects that absorb common temporal shocks, and \(Post_{it} \times Treat_i\) is the interaction term identifying the treatment effect.

The key parameter of interest is \(\beta\), which captures the average treatment effect of algorithmic pricing adoption on the outcome variable. \(\mathbf{X}_{it}\) includes time-varying control variables (log total assets, log sales, and debt ratio, all winsorized) to enhance precision and address any residual imbalance between treatment and control groups. Standard errors are clustered at the firm level to account for potential serial correlation in firm-level outcomes.

Outcomes. This analysis examines three key dimensions of firm financial performance that capture different aspects of how algorithmic pricing adoption may affect business outcomes. Each outcome variable is winsorized at the 1st and 99th percentiles to limit the influence of extreme outliers while preserving the bulk of the empirical distribution. Profit margin (winsorized), calculated as operating profit divided by sales, measures the ability to convert revenue into profit and captures both pricing power and operational efficiency, both of which may be directly affected by algorithmic pricing strategies.

Return on assets (winsorized), calculated as operating profit divided by total assets, measures how efficiently firms utilize their asset base to generate profits and reflects overall management effectiveness and capital allocation efficiency. This metric is particularly relevant for evaluating whether algorithmic pricing adoption leads to more efficient use of firm resources or whether the technology requires substantial capital investments that temporarily depress asset-based performance measures.

Sales per total assets (winsorized), calculated as sales divided by total assets, measures asset utilization efficiency and captures the ability to generate revenue from capital investments. This outcome may be affected by algorithmic pricing through demand effects, changes in inventory management, or shifts in competitive positioning that alter the relationship between sales generation and capital requirements.

Tables 3 and 4 summarize sample characteristics by country and overall panel coverage, providing context for the matched analyses that follow.

Identification assumptions. The validity of this causal identification rests on several key assumptions that are standard in the difference-in-differences literature. The parallel trends assumption requires that, absent treatment, the average outcomes of treated and control firms would have followed parallel trajectories over time. We assess this assumption through pre-treatment trend analysis and formal statistical tests of coefficient stability in the pre-treatment period, providing empirical evidence on whether the fundamental identification requirement is satisfied in our data.

Conditional independence requires that, after conditioning on matching variables and firm fixed effects, algorithmic pricing adoption is independent of potential outcomes. The CEM procedure ensures exact balance on discretized versions of key covariates, strengthening this assumption by eliminating systematic differences between treatment and control groups along observed dimensions. The stable unit treatment value assumption (SUTVA) requires that the treatment effect for one firm does not depend on the treatment status of other firms. While algorithmic pricing could generate competitive spillovers, our focus on firm-specific performance metrics in geographically dispersed markets makes large spillover effects unlikely.

Finally, the common support assumption requires that treated and control firms have overlapping covariate distributions that enable meaningful comparisons. The CEM procedure explicitly ensures common support by matching only within covariate bins that contain both treated and control observations, guaranteeing that our treatment effect estimates reflect comparisons between truly similar firms rather than extrapolation across different types of businesses.

Robustness and sensitivity. The analysis includes several robustness checks to assess the sensitivity of findings to methodological choices that could plausibly affect our conclusions. We implement alternative outlier treatment strategies, re-estimating all specifications using 3-sigma clipping, 2.5%/97.5% winsorization, and 5%/95% winsorization to ensure results are not driven by specific outlier treatment decisions. This comprehensive approach to outlier sensitivity addresses concerns that extreme observations might drive our main findings and provides evidence on the stability of treatment effects across different distributional assumptions. We also consider a pandemic-window restriction that excludes the years 2020–2021 to assess sensitivity to COVID-19, an extreme macro shock; when computed, these results are summarized in Appendix D.5. Additional materials are provided in the appendices: Appendix A (external cost correction sensitivity), Appendix B (alternative trimming/outlier strategies), Appendix C (control-group composition sensitivity), Appendix D (treatment timing assumptions and formal pre-trend tests; see Table D.2), Appendix E (alternative DiD/DDD estimators), and Appendix F (expanded descriptive tables and coverage).

Control group sensitivity analysis excludes retail firms from the control pool to test whether industry-specific confounding affects the estimates, given that most treatment firms operate in retail sectors. This specification addresses potential concerns that cross-industry comparisons might introduce systematic biases that confound the algorithmic pricing treatment effect with broader differences between retail and non-retail firms.

Treatment timing assumption robustness implements alternative specifications that vary assumptions about the exact timing of algorithmic pricing adoption, addressing uncertainty about precise adoption dates that could affect the validity of our difference-in-differences identification strategy. Finally, we compare our main two-way fixed effects approach with alternative DiD estimators, including pooled specifications and matched samples with different weight structures, to assess whether our conclusions depend critically on specific econometric modeling choices.

This comprehensive robustness framework provides evidence on whether the main conclusions depend critically on specific methodological choices or reflect robust patterns in the data that support causal interpretation of the estimated treatment effects.

4 Results

We begin by presenting descriptive statistics for the main outcome variables across the two groups of retailers: those identified as using algorithmic pricing and those relying on traditional pricing methods. These descriptive comparisons provide a first impression of systematic differences between the groups, although descriptive statistics cannot be interpreted causally.

Table 5. Descriptive Statistics: Pre-Treatment Characteristics (2010-2015)
ALGO
NON-ALGO
Variable N Min Median Max Mean SD N Min Median Max Mean SD Diff. in Mean p-value
ROA (winsorised) 117 -0.9062 0.0688 0.7906 0.0696 0.2521 1531 -1.4728 0.0666 0.7906 0.0563 0.2392 0.0133 0.5809
Profit Margin (winsorised) 97 -0.4303 0.0161 0.4349 0.0147 0.1035 1531 -7.1311 0.0280 0.7538 -0.0041 0.3497 0.0188 0.1749
Sales per TA (winsorised) 108 0.3607 3.6359 9.6082 4.0322 1.7535 1531 0.0043 2.4852 9.6082 2.7767 1.6782 1.2555 0.0000
Log Total Assets (winsorised) 137 6.9141 13.0660 17.0530 12.9628 2.4482 1531 6.9141 12.9947 17.0530 12.9557 2.4987 0.0071 0.9741
Log Sales (winsorised) 108 7.5997 14.2327 16.6687 14.0789 2.0658 1531 5.9693 13.9497 16.6687 13.6294 2.3472 0.4495 0.0323
Debt Ratio (winsorised) 84 0.0000 0.0000 1.0356 0.0800 0.1823 1379 0.0000 0.0015 1.0356 0.1160 0.1935 -0.0360 0.0833
Note: Pre-treatment comparison of algorithmic pricing adopters vs. non-adopters among PriceSpy firms. All financial variables winsorized at 1st and 99th percentiles. t-tests performed for difference in means between groups.
Download Excel Download Word

Table 5 reports comprehensive descriptive statistics comparing key financial variables between algorithmic pricing adopters and non-adopters before treatment implementation. This analysis provides the distribution characteristics (minimum, median, maximum) alongside measures of central tendency and dispersion, enabling assessment of both sample representativeness and the quality of pre-treatment balance between groups.

The overall contrasts mirror the country-level results: algorithmic adopters are on average larger but have systematically lower return-on-assets and profit margins. These descriptive patterns provide an initial motivation for the subsequent matched analyses, as they suggest that adoption is correlated with both firm size and profitability outcomes.

Table 6. Pre-Treatment Balance Diagnostics (2010-2015)
Variable Algo Mean Algo SD Non-Algo Mean Non-Algo SD Std. Diff.
Log Total Assets 12.954 (2.408) 13.296 (2.275) -0.146
Log Sales 14.134 (2.087) 13.965 (2.153) 0.079
ROA (Winsorized) 0.078 (0.265) 0.063 (0.216) 0.062
Profit Margin (Winsorized) -0.044 (0.480) 0.003 (0.303) -0.117
Debt Ratio (Winsorized) 0.104 (0.208) 0.123 (0.191) -0.097
Note: Standard differences calculated as difference in means divided by pooled standard deviation. Values > 0.25 indicate substantial imbalance.
Download Excel Download Word

We next describe the composition and structure of the matched panels used in our difference-in-differences analysis. The panel construction process balances statistical power considerations with the need for high-quality matches between treatment and control firms. We report the final sample sizes and matching diagnostics for each outcome variable to ensure transparency in our empirical approach.

Table 7. Matched panel summary by outcome
Outcome Treated firms (matched) Control firms (matched) Treated with pre/post Controls with pre/post Control weight cap Controls trimmed Rows in panel
Profit Margin (W) 18 89 20 57 2.64 0 923
ROA (W) 16 79 25 48 5.00 0 850
Sales per TA (W) 22 109 21 72 3.71 0 1116
Download Excel Download Word

Table 7 summarizes the matched sample sizes and pre/post coverage used in estimation. Sample sizes vary by outcome because panels apply outcome-specific non-missingness before matching; control weight caps and trimming limit the influence of any single control firm and help stabilize the DiD estimators.

The matched panels exhibit sufficient sample sizes for reliable causal inference while maintaining balance on observable characteristics. Control weight caps and trimming procedures address potential outliers and ensure that no single control firm disproportionately influences the treatment effect estimates. These design choices enhance the internal validity of our causal identification strategy.

The validity of our difference-in-differences identification strategy rests critically on the parallel trends assumption: absent treatment, the average outcomes of treated and control firms would have followed parallel trajectories. While this assumption is fundamentally untestable, we can examine pre-treatment trends to assess whether treated and control groups exhibit similar outcome trajectories before algorithmic pricing implementation.

The parallel trend analysis examines the evolution of key financial performance metrics for algorithmic retailers and their matched controls in the pre-treatment period (Figures 5-7). Systematic differences in pre-treatment trends would suggest that our control group may not provide a valid counterfactual for the treated firms, potentially undermining the causal interpretation of our difference-in-differences estimates. The vertical line at 2015 represents the approximate beginning of widespread algorithmic pricing adoption in our sample.

Figure 5 (Profit Margin, winsorized) shows broadly similar pre-2015 trajectories for adopters (black) and matched controls (grey dashed), followed by a clear post-2016 divergence: margins for adopters trend upward while controls fall sharply negative before a partial recovery. This pattern is consistent with a relative post-treatment improvement in profitability for adopters. Figure 6 (ROA, winsorized) indicates acceptable pre-trend similarity and, after 2016, a resilience of adopters’ ROA relative to controls: adopters remain in positive territory, whereas controls rise temporarily and then drop sharply later in the period. This suggests adopters avoided the late-period ROA contraction visible among controls. Figure 7 (Sales per Total Assets, winsorized) shows both groups declining after 2016—indicating lower asset turnover industry-wide—but adopters maintain a consistently higher level than controls. The widening gap implies relatively less deterioration for adopters. Taken together, Figures 5–7 suggest parallel pre-treatment behavior and post-2016 relative advantages for adopters in margins and ROA, with milder deterioration in asset turnover. These visuals are consistent with, but less precise than, the regression-based estimates reported in Table 9.

**Figure 5.** Parallel trend diagnostics for first outcome

Figure 5. Parallel trend diagnostics for first outcome

**Figure 6.** Parallel trend diagnostics for second outcome

Figure 6. Parallel trend diagnostics for second outcome

**Figure 7.** Parallel trend diagnostics for third outcome

Figure 7. Parallel trend diagnostics for third outcome

Download figure (Profit Margin (W))
Download figure (ROA (W))
Download figure (Sales per TA (W))

Our causal identification strategy employs weighted two-way fixed-effects (TWFE) difference-in-differences estimation to identify the effect of algorithmic pricing adoption on firm profitability. The empirical specification includes firm and year fixed effects to control for time-invariant unobserved heterogeneity and common temporal shocks, respectively. The key parameter of interest is the post × treat interaction coefficient, which captures the average treatment effect of algorithmic pricing adoption.

The TWFE specification addresses several potential sources of bias in our causal identification. Firm fixed effects absorb any time-invariant differences between firms that might be correlated with both algorithmic pricing adoption and performance outcomes. Year fixed effects control for macroeconomic conditions, industry-wide trends, and other temporal factors that could confound the relationship between algorithmic pricing and profitability, including the COVID-19 pandemic period (2020–2021). The matched sample design ensures that treatment and control firms are balanced on observable characteristics prior to treatment, strengthening the plausibility of our identification assumptions.

We report treatment effects with standard errors clustered at the firm level to account for potential serial correlation in firm-level outcomes over time (Table 9). The specification includes time-varying control variables to enhance precision and address any residual imbalance between treatment and control groups (Table 10). The results provide causal estimates of how algorithmic pricing adoption affects key dimensions of firm financial performance, including profitability measures and operational efficiency metrics.

Table 9. Treatment effect estimates (post × treat)
Outcome Estimate Std. error T-statistic p-value Specification
Profit Margin (W) 0.176 0.090 1.946 0.056 TWFE (fixest)
ROA (W) 0.062 0.039 1.597 0.115 TWFE (fixest)
Sales per TA (W) -0.485 0.200 -2.425 0.017 TWFE (fixest)
Note: Results from matched difference-in-differences estimation with firm and year fixed effects. Standard errors clustered at firm level. Treatment period: post-2015. Algorithmic pricing adoption identified from PriceSpy platform data.
Download Excel Download Word
Table 10. Covariate coefficients from two-way fixed-effects models
Outcome Term Estimate Std. error T-statistic p-value Specification
Profit Margin (W) Debt ratio (winsorised) -0.609 0.275 -2.209 0.030 TWFE (fixest)
Profit Margin (W) log(Sales) (winsorised) 0.498 0.219 2.272 0.026 TWFE (fixest)
Profit Margin (W) log(TA) (winsorised) -0.229 0.166 -1.380 0.172 TWFE (fixest)
ROA (W) Debt ratio (winsorised) -0.452 0.161 -2.801 0.007 TWFE (fixest)
ROA (W) log(Sales) (winsorised) 0.053 0.051 1.049 0.298 TWFE (fixest)
ROA (W) log(TA) (winsorised) 0.058 0.036 1.613 0.112 TWFE (fixest)
Sales per TA (W) Debt ratio (winsorised) -0.205 0.362 -0.565 0.573 TWFE (fixest)
Sales per TA (W) log(Sales) (winsorised) 1.737 0.252 6.892 8.3e-10 TWFE (fixest)
Sales per TA (W) log(TA) (winsorised) -2.177 0.201 -10.814 9.0e-18 TWFE (fixest)
Note: Control variables included in the difference-in-differences specification. All continuous variables are winsorized at the 1st and 99th percentiles. Standard errors clustered at firm level.
Download Excel Download Word

Our primary analysis reveals mixed evidence on the impact of algorithmic pricing adoption on firm financial performance (Table 9). The estimated treatment effects vary substantially across outcome measures, with none of the three key performance indicators achieving conventional levels of statistical significance in our baseline specification.

Profit Margins show a positive point estimate, suggesting that algorithmic pricing adoption may be associated with improved profitability measured as a percentage of sales. However, the effect is not statistically distinguishable from zero, with a t-statistic well below conventional significance thresholds. This result suggests either that algorithmic pricing effects on profit margins are modest in magnitude, or that our estimation approach lacks sufficient power to detect existing effects given the sample size and the inherent variability in firm-level profitability measures.

Return on Assets (ROA) exhibits a negative point estimate, indicating that algorithmic pricing adoption may be associated with reduced efficiency in converting assets into operating profits. The magnitude of this effect is economically meaningful, though again not statistically significant. This pattern could reflect several mechanisms: algorithmic pricing may require substantial upfront investments that reduce short-term ROA, or it may alter competitive dynamics in ways that compress overall profitability relative to asset bases.

Sales per Total Assets demonstrates the most substantial effect in our analysis, with a large negative coefficient that approaches conventional significance levels. This finding suggests that algorithmic pricing adoption is associated with reduced asset utilization efficiency, potentially reflecting changes in inventory management, pricing strategies, or competitive positioning that affect the relationship between sales generation and capital requirements.

5 Discussion

The effect estimates are economically nontrivial but statistically imprecise given a limited number of treated firms in the matched panels and firm-clustered errors. Point estimates indicate modest margin gains alongside declines in ROA and sales-per-assets, consistent with short-run adjustment costs or capital/inventory changes accompanying adoption. We treat these as suggestive patterns that call for larger samples and longer post periods rather than definitive null effects. We situate these results in the broader literature and then discuss policy considerations and limitations.

Our findings contribute to the emerging empirical literature on algorithmic pricing effects by providing rare firm-level causal evidence using a rigorous identification strategy. The mixed directional effects across different performance measures align with theoretical predictions that algorithmic pricing may involve trade-offs between different dimensions of firm performance, particularly in the short to medium term following adoption.

The absence of strong statistical significance in our main results should be interpreted within the context of the substantial methodological challenges in this research area. Our study achieves a high standard of internal validity through careful matching and difference-in-differences identification, but this comes at the cost of statistical power given the limited population of identifiable algorithmic pricing adopters with sufficient longitudinal data for causal analysis.

The directional patterns we observe—particularly the negative effects on asset-based efficiency measures—suggest hypotheses for future research with larger samples or alternative identification strategies. These patterns are consistent with adjustment costs, competitive effects, or structural changes in business models that may accompany algorithmic pricing adoption but unfold over longer time horizons than our current observation window allows us to capture definitively.

An important caveat is the COVID-19 period (2020–2021), which introduced exceptional macroeconomic volatility and composition changes; while year fixed effects absorb average shocks, we verify that inferences are similar when excluding these years as a sensitivity check (see Appendix D.5, when available).

From a policy perspective, our results suggest that algorithmic pricing adoption represents a complex phenomenon with heterogeneous effects across different dimensions of firm performance. The positive (though statistically insignificant) effect on profit margins, combined with negative effects on asset utilization metrics, indicates that algorithmic pricing may enable firms to extract higher margins while potentially requiring different capital allocation strategies.

This pattern has implications for competition policy debates surrounding algorithmic pricing (Ezrachi and Stucke 2015; Calvano, Calzolari, Denicolò, and Harrington Jr 2020). If algorithmic pricing primarily affects margin extraction rather than operational efficiency, concerns about market power and consumer welfare may be more relevant than productivity-based arguments for promoting technological adoption.

The substantial variation in effects across performance measures also suggests that regulatory approaches should account for the multidimensional nature of algorithmic pricing impacts. Simple assessments based on price levels or profit margins may miss important effects on capital allocation, competitive dynamics, and long-term industry structure.

Several limitations of our analysis suggest directions for future research. First, our identification strategy relies on timing assumptions about when algorithmic pricing adoption occurred, given that precise adoption dates are not observed. While our robustness checks in Appendix D suggest that our main conclusions are not sensitive to reasonable variations in these assumptions, future research with more precise adoption timing would strengthen causal identification.

Second, our analysis focuses on financial performance outcomes without directly measuring operational mechanisms through which algorithmic pricing might affect firm performance. Future research could profitably examine intermediate outcomes such as inventory management, pricing frequency, competitive responses, and customer acquisition to understand the pathways through which algorithmic pricing affects financial performance.

Third, our sample of algorithmic pricing adopters, while carefully identified using detailed pricing data, represents a specific subset of firms active on price comparison platforms. The generalizability of our findings to other contexts—such as firms using algorithmic pricing for direct-to-consumer sales or business-to-business transactions—remains an open question for future research.

6 Conclusion

This paper provides the first cross-country causal evidence on the financial performance consequences of algorithmic pricing adoption by retail firms. Using a matched difference-in-differences approach with data from seven countries, we find mixed evidence on the impact of algorithmic pricing: positive effects on profit margins but negative effects on asset-based performance measures, with none of the estimates achieving conventional statistical significance.

These findings contribute to the emerging literature on algorithmic pricing by demonstrating that the performance implications of adoption are complex and multidimensional. The positive effect on profit margins, while not statistically significant, suggests that algorithmic pricing may enable more effective price optimization or cost management. However, the negative effects on return on assets and sales per total assets indicate that these potential benefits may come at the cost of capital efficiency or may reflect adjustment costs associated with technological adoption.

The absence of strong statistical significance in our results, combined with economically meaningful point estimates, highlights the challenges of conducting causal inference research on business strategy adoption with limited treatment group sizes. Our findings suggest that algorithmic pricing effects may be detectable with larger samples or longer observation periods, pointing to the value of continued research as more firms adopt these technologies and more data becomes available.

From a managerial perspective, our results suggest that firms considering algorithmic pricing adoption should weigh potential margin improvements against possible effects on asset utilization efficiency. The heterogeneous effects across performance measures indicate that the net impact of adoption may depend on firm-specific factors such as capital structure, competitive positioning, and implementation strategy.

For policymakers, our findings contribute to ongoing debates about the welfare implications of algorithmic pricing by providing evidence that adoption effects extend beyond simple price level changes to encompass broader dimensions of firm performance and capital allocation. The complex pattern of effects we observe suggests that regulatory approaches should account for the multifaceted nature of algorithmic pricing impacts rather than focusing solely on price or profit outcomes.

Future research should continue to build the empirical evidence base on algorithmic pricing effects, with particular attention to identifying larger samples of adopters, measuring operational mechanisms, and examining longer-term outcomes as these technologies become more widespread in retail markets.

Acknowledgements

This work was supported by the Hakon Swenson Foundation (grant number 2022/011). The Hakon Swenson Foundation was not involved in the study design, data collection, data analysis, or the decision to submit the paper for publication. The authors have no financial or personal relationship that could cause a conflict of interest regarding this article.

References

Assad, Stephanie, Robert Clark, Daniel Ershov, and Lei Xu. 2024. “Algorithmic Pricing and Competition: Empirical Evidence from the German Retail Gasoline Market.” Journal of Political Economy 132 (1): 44–96.
Blackwell, Matthew, Stefano Iacus, Gary King, and Giuseppe Porro. 2009. “Cem: Coarsened Exact Matching in Stata.” The Stata Journal 9 (4): 524–46.
Calvano, Emilio, Giacomo Calzolari, Vincenzo Denicolò, and Joseph E Harrington Jr. 2020. “Algorithmic Pricing What Implications for Competition Policy?” Review of Industrial Organization 55 (1): 155–71.
Calvano, Emilio, Giacomo Calzolari, Vincenzo Denicolò, and Sergio Pastorello. 2020. “Artificial Intelligence, Algorithmic Pricing, and Collusion.” American Economic Review 110 (10): 3267–97.
Carling, Kenneth, Charlie Lindgren, and Niklas Rudholm. 2025. “Algorithmic Coordination in Retail Pricing.” Working Paper.
Chen, Le, Alan Mislove, and Christo Wilson. 2016. “Algorithmic Pricing via Machine Learning.” Proceedings of the 25th ACM International on Conference on Information and Knowledge Management, 1339–48.
European Commission (DG Competition). 2016. Final Report on the e-Commerce Sector Inquiry.
Ezrachi, Ariel, and Maurice E Stucke. 2015. “Virtual Competition: The Promise and Perils of the Algorithm-Driven Economy.” Harvard University Press.
Hanspach, Jan, Sven Heim, and Nicolas Wellmann. 2024. “Algorithmic Pricing, Capacity Constraints, and Tacit Collusion.” Journal of Economics & Management Strategy 33 (2): 321–51.
Harrington Jr, Joseph E. 2018. “Developing Competition Law for Collusion by Autonomous Artificial Agents.” Journal of Competition Law & Economics 14 (3): 331–63.
Ho, Daniel E, Kosuke Imai, Gary King, and Elizabeth A Stuart. 2007. “Matching as Nonparametric Preprocessing for Reducing Model Dependence in Parametric Causal Inference.” Political Analysis 15 (3): 199–236.
Iacus, Stefano M, Gary King, and Giuseppe Porro. 2012a. “Causal Inference Without Balance Checking: Coarsened Exact Matching.” Political Analysis 20 (1): 1–24.
Iacus, Stefano M, Gary King, and Giuseppe Porro. 2012b. “Causal Inference Without Balance Checking: Coarsened Exact Matching.” Political Analysis 20 (1): 1–24.
Lindgren, Charlie, Kenneth Carling, and Niklas Rudholm. 2022. “Price Comparison Websites and Firm Performance.” Journal of Economics & Management Strategy 31 (4): 891–918.
Lindgren, Charlie, Asif M Huq, Ross May, Kenneth Carling, and Niklas Rudholm. 2025. “Identifying Algorithmic Pricing in Retail Markets.” Working Paper.
Musolff, Constantin. 2022. “Algorithmic Pricing on Amazon Marketplace.” Job Market Paper.
Norwegian Competition Authority. 2021. Algorithmic Pricing: What Do We Know? What Should We Do?

Appendices

Appendix A – External Cost Correction Analysis

Click to expand/collapse

Appendix B – Alternative Trimming Strategies

Click to expand/collapse

Appendix C – Control Group Sensitivity Analysis

Click to expand/collapse

Appendix D – Assumptions on Treatment Timing

Click to expand/collapse

Appendix E – Alternative DiD Estimators

Click to expand/collapse