Abstract: Algorithmic pricing is increasingly deployed in retail markets, raising questions about its broader consequences for firm performance. This paper investigates whether retailers that employ algorithmic pricing differ in profitability, efficiency, and growth compared with otherwise similar non-adopters. We compile a multi-country firm-year panel linking retailer presence on a major price comparison platform to financial accounts across multiple European countries. For retailers on the price comparison platform, algorithmic pricers have been identified using a novel heuristic. To address the non-random nature of adoption, we construct matched samples of adopters and non-adopters based on pre-treatment characteristics and estimate treatment effects using matched difference-in-differences designs. The analysis focuses on four financial outcomes: return on assets, total asset turnover, sales growth, and profit margin. Results suggest mixed evidence on the impact of algorithmic pricing adoption, with positive effects on profit margins but negative effects on asset-based performance measures. These findings contribute to the emerging literature on algorithmic pricing by providing rare firm-level causal evidence using a rigorous identification strategy.

Keywords: Algorithmic pricing; Online retail; Profitability; Causal inference; Matching methods

JEL classifications: L11; L81; C21; D22

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. 2016a; 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. Putting it plainly, if a retailer is consistently active in a market and changes prices across many products so frequently that such behaviour could not reasonably be managed by hand, the combination of high market presence and high pricing frequency indicates the use of algorithmic pricing. In the present study, we examine whether retailers that employ algorithmic pricing differ systematically in return on assets, total asset turnover, sales growth, and profit margins compared with 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 multi-country 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 employs a difference-in-differences design with coarsened exact matching (Blackwell et al. 2009; Iacus et al. 2012), treating algorithmic pricing adoption as occurring around 2015. This approach reflects a key data limitation: while Lindgren et al. (2025) identifies which retailers are algorithmic adopters based on their pricing behavior observed in 2023–2024, we do not observe the precise date when each firm adopted algorithmic pricing. Drawing on the diffusion timeline documented in Lindgren et al. (2025) and related industry reports (Norwegian Competition Authority 2021), we partition our panel into a pre-treatment period (2010–2015) and a post-treatment period (2016–2023), under the assumption that widespread adoption began around 2015–2016. This classification treats each firm as consistently algorithmic or non-algorithmic throughout the observation window—an approximation necessitated by the absence of adoption dates, but one that allows us to estimate average treatment effects for early adopters relative to comparable non-adopters. We focus on four key financial outcomes: return on assets, total asset turnover, sales growth, and profit margin.

The remainder of the paper is structured as follows. Section 2 presents the data, including details on standardization, 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) identifies algorithmic pricing adopters based on systematic analysis of pricing patterns from the PriceSpy platform during 2020–2022. These firms—our treatment group—represent retailers that have implemented algorithmic pricing solutions and for whom we can observe both pre- and post-adoption financial performance. The algorithmic adopters are then linked to firm‑year financial accounts to construct a multi‑country panel suitable for comparing their outcomes against two potential control pools: (i) non‑algorithmic retailers also present on PriceSpy, and (ii) the broader universe of firms with comparable financial accounts. The panel spans 2010–2024, with coverage varying by 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 standardization process 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.

Financial data quality required systematic cleaning and validation across multiple accounting standards and reporting conventions. We first corrected implausible entries (e.g., negative cost of goods sold, sales exceeding total assets) and removed observations missing essential variables (total assets, operating profit, or sales). Accounting logic violations—such as inconsistent balance sheet identities or impossible financial ratios—were flagged and excluded following standard data quality protocols.

From the cleaned accounts, we constructed standardized performance measures including return on assets (ROA), profit margins, sales per total assets (asset turnover), debt ratios, and inventory turnover. To limit the influence of extreme outliers while preserving the empirical distribution, all continuous financial variables were winsorized at the 1st and 99th percentiles within each country-year cell. This approach ensures that extreme values do not disproportionately influence our estimates while maintaining cross-country comparability. Alternative outlier treatment strategies—including 3-sigma clipping and more aggressive winsorization at the 2.5th/97.5th and 5th/95th percentiles—are examined systematically in Appendix B to verify that our main conclusions are robust to these methodological choices.

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 standardization pipeline prior to currency conversion, scaling, and panel‑wide cleaning.

Table 1. Sample Selection and Data Processing Flow
Stage Count (firm-years unless noted)
Initial raw data observations 9,322,530
Less: Exclusions after data quality review 154,935
After problematic record removal 9,167,595
Less: Insufficient financial data coverage 2,073,088
Final analytical sample 7,094,507
Final sample composition (unique firms):
• Treatment group (algorithmic pricing retailers on PriceSpy) 66 firms
• PriceSpy control group (non-algorithmic retailers on PriceSpy) 641 firms
• General control pool (all other firms not on PriceSpy) 1,040,800 firms
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Table 1 summarizes the sample selection and data processing flow from raw observations to the final analytical panel. The final sample composition distinguishes three groups: algorithmic pricing retailers on PriceSpy (our treatment group), non-algorithmic retailers on PriceSpy, and all other firms not on PriceSpy. Our main analysis draws controls from the full general control pool to maximize statistical power through coarsened exact matching. Appendix C examines robustness by excluding retail firms from the control pool to test whether control group contamination affects our findings.

Table 2. Sample construction by country, year, and adoption group
Group Country 2010 2011 2012 2013 2014 2015 2016 2017 2018 2019 2020 2021 2022 2023 2024 Total
Treatment Denmark 4 2 4 6 5 7 6 7 6 8 8 8 6 7 7 91
Finland - - - - - - - - - - - - - - - -
France 0 0 0 0 0 0 0 0 0 1 1 1 1 1 2 7
Norway 3 2 5 7 6 6 6 6 6 7 8 7 6 6 7 88
Sweden 11 12 13 13 13 14 16 17 17 16 17 20 20 20 2 221
UK 0 0 0 0 2 2 2 4 6 7 7 9 9 8 4 60
Total 18 16 22 26 26 29 30 34 35 39 41 45 42 42 22 467
Control Denmark 3 9 152 312 428 563 608 629 666 671 637 695 769 777 569 7488
Finland 9 35 195 1020 1256 1381 1592 1779 1926 2106 2297 2409 2519 2464 1345 22333
France 778 4277 7495 8710 10164 12008 12522 12054 11876 11841 11950 12040 13836 24769 27591 181911
Norway 2 153 1241 2227 3195 3518 3871 4191 4466 4800 5189 5423 5411 4685 3048 51420
Sweden 244067 263679 275687 287769 302314 315118 329405 342569 354672 366529 384260 402300 420008 409200 46 4697623
UK 29 54 91 414 4298 5941 6850 7088 7029 7224 7394 7731 7940 6356 4941 73380
Total 244888 268207 284861 300452 321655 338529 354848 368310 380635 393171 411727 430598 450483 448251 37540 5034155
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Table 2 reports the number of firms with available financial data by country and year, distinguishing treatment firms (algorithmic pricing adopters) from all control firms (both PriceSpy retailers and the broader universe of firms with financial accounts). The table provides transparency about the underlying data structure: when firms first appear in the financial records, how coverage evolves over time, and the relative scale of treatment versus control observations. Treatment firms represent a small fraction of the total sample, reflecting the fact that algorithmic pricing adoption is concentrated among a subset of retailers operating on the PriceSpy platform, while the control pool comprises both non-algorithmic PriceSpy retailers and the much larger universe of firms not listed on the platform. The temporal patterns show data availability increasing over time as more firms file financial reports through the various national registries and data sources used in this study.

Table 3. Sample Characteristics by Country and Treatment Status
Group Country 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]
Treatment Denmark 14 114 0.131 (0.271) [76] 0.020 (0.008) [12] 4.553 (0.599) [14] 0.163 (0.127) [10] 13.897 (2.769) [114]
Finland 0 0 – – [0] – – [0] – – [0] – – [0] – – [0]
France 2 7 0.117 (0.031) [7] 0.025 (0.010) [7] 4.916 (0.730) [7] 0.183 (0.237) [5] 7.059 (0.221) [7]
Norway 11 88 0.046 (0.481) [66] 0.059 (0.212) [66] 4.915 (2.944) [87] 3.124 (4.922) [77] 13.052 (2.126) [88]
Sweden 31 306 0.000 (0.295) [306] -0.069 (0.585) [306] 3.389 (1.640) [306] 0.377 (1.481) [277] 12.626 (2.454) [306]
UK 9 60 0.082 (0.264) [53] -0.026 (0.442) [53] 3.370 (1.193) [53] 0.289 (1.617) [45] 13.561 (3.250) [60]
Control Denmark 35 183 0.005 (0.423) [183] 0.015 (0.214) [183] 2.905 (1.757) [183] 0.502 (2.145) [148] 13.589 (3.269) [183]
Finland 10 85 0.035 (0.113) [85] 0.002 (0.065) [85] 3.815 (2.591) [85] 0.081 (0.348) [75] 9.603 (1.925) [85]
France 21 129 0.066 (0.171) [129] -0.035 (0.386) [129] 2.238 (1.049) [129] 0.082 (0.248) [108] 9.808 (2.658) [129]
Norway 32 293 0.114 (0.162) [293] 0.047 (0.077) [293] 2.801 (1.276) [293] 0.092 (0.421) [261] 8.800 (1.710) [293]
Sweden 503 5015 0.056 (0.212) [5015] -0.004 (0.317) [5015] 2.764 (1.669) [5015] 0.356 (1.422) [4533] 13.152 (2.266) [5015]
UK 40 226 0.141 (0.270) [226] 0.035 (0.502) [226] 2.484 (1.596) [226] 0.049 (0.289) [186] 10.678 (3.032) [226]
Note: 'Est.' columns show Mean (Standard Deviation), '[N]' columns show [Number of Observations]. Treatment = firms using algorithmic pricing; Control = traditional pricing firms.
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Table 3 compares core financial metrics by country and treatment status for PriceSpy retailers, reporting mean (standard deviation) and the number of observations. The 67 treatment firms (algorithmic pricing adopters) are substantially outnumbered by 641 control firms (non-algorithmic retailers on PriceSpy), but exhibit markedly different operational characteristics. Across the pooled sample, treatment firms demonstrate higher asset turnover (3.87 vs. 2.76), indicating more intensive use of their asset base to generate sales. However, algorithmic adopters show lower return on assets (4.3% vs. 6.1%) and slightly negative profit margins (−2.7% vs. 0.0%), suggesting that operational intensity does not translate directly into superior profitability in the raw data. Treatment firms are also somewhat larger on average (log total assets of 12.97 vs. 12.73), though substantial within-group variation exists across countries. These descriptive statistics reveal systematic differences in firm characteristics between algorithmic pricing adopters and non-adopters that motivate the use of matching methods to construct comparable treatment and control groups for causal inference.

Table 4. Panel coverage by country and firm type
Country Treatment: Firms Treatment: Firm-years PriceSpy: Firms PriceSpy: Firm-years Other: Firms Other: Firm-years
Denmark 14 114 35 183 1224 7305
Finland 0 0 10 85 3390 22248
France 2 7 21 129 41163 181782
Norway 11 88 32 293 6827 51127
Sweden 31 306 503 5015 974160 6752385
UK 9 60 40 226 14045 73154
Total 66 575 641 5931 1040800 7088001
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Table 4 reports the number of firms and firm-year observations by country in the panel. The total row clarifies the aggregate scale for subsequent analyses and helps contextualize the sample sizes used in the balance diagnostics (Appendix F, Table F.1) and the DiD estimates (Table 6).

The resulting dataset is a standardized firm-year panel with algorithmic pricing status in the 2020-2023 period 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 profit margin, return on assets, sales, and asset turnover (sales per total assets).

**Figure 1.** Number of treatment and control group firms with financial data available by year (2010–2023)

Figure 1. Number of treatment and control group firms with financial data available by year (2010–2023)

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Figure 1 documents the staggered reporting for the treatment and control group firms in our dataset, with cumulative counts rising unevenly over time. This staggered appearance of treatment group firms in the annual report data has two implications for design and interpretation. First, matching: because treated and control group firms start supplying annual reports via the chosen sources enter 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.

Table 5. Descriptive Statistics: Pre- and Post-Treatment Characteristics
Treatment
Control
Period Variable N Median Mean SD N Median Mean SD Diff. in Mean p-value
Pre-treatment (2010-2015) ROA (winsorised) 117 0.0688 0.0696 0.2521 1531 0.0666 0.0563 0.2392 0.0133 0.5809
Profit Margin (winsorised) 97 0.0161 0.0147 0.1035 1531 0.0280 -0.0041 0.3497 0.0188 0.1749
Sales per TA (winsorised) 108 3.6359 4.0322 1.7535 1531 2.4852 2.7767 1.6782 1.2555 0.0000
Log Total Assets (winsorised) 137 13.0660 12.9628 2.4482 1531 12.9947 12.9557 2.4987 0.0071 0.9741
Log Sales (winsorised) 108 14.2327 14.0789 2.0658 1531 13.9497 13.6294 2.3472 0.4495 0.0323
Debt Ratio (winsorised) 84 0.0000 0.0800 0.1823 1379 0.0015 0.1160 0.1935 -0.0360 0.0833
Post-treatment (2016-2023) ROA (winsorised) 175 0.0838 0.1029 0.1961 325597 0.0876 0.0829 0.3277 0.0200 0.1790
Profit Margin (winsorised) 159 0.0236 0.0403 0.1298 325591 0.0653 -0.1448 1.3973 0.1851 0.0000
Sales per TA (winsorised) 159 3.1286 3.5453 1.9713 325591 1.3538 1.7719 1.7278 1.7734 0.0000
Log Total Assets (winsorised) 175 12.9716 12.9555 2.5218 325597 11.1244 11.6346 1.9039 1.3209 0.0000
Log Sales (winsorised) 159 13.4403 13.2644 2.4778 325591 11.5754 11.5702 2.1729 1.6943 0.0000
Debt Ratio (winsorised) 102 0.0000 0.0541 0.1434 325591 0.0000 0.0455 0.1406 0.0086 0.5474
Note: Comparison of treatment group (algorithmic pricing adopters) vs. control group across pre-treatment (2010-2015, unmatched PriceSpy firms) and post-treatment (2016-2023, matched sample after CEM) periods. Median, mean, and standard deviation reported for each group. All financial variables winsorized at 1st and 99th percentiles. t-tests performed for difference in means between groups.
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Table 5 reports comprehensive descriptive statistics comparing key financial variables between treatment and control firms across both pre-treatment (2010-2015) and post-treatment (2016-2023) periods. The pre-treatment comparison uses unmatched PriceSpy firms to document the raw differences between algorithmic pricing adopters and non-adopters before implementation, revealing that adopters are on average larger but have systematically lower return-on-assets and profit margins. The post-treatment comparison uses the matched sample constructed through coarsened exact matching, showing how the relative performance evolved after algorithmic pricing adoption. Comparing the treatment-control gaps across periods provides insight into both the initial selection into algorithmic pricing adoption and the subsequent causal effects of the technology on firm performance.

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. Since we know treatment status in the 2020 to 2023 period based on Lindgren et al. (2025), all treatment group firms are assumed to have implemented algo pricing after 2013, but before 2020. The control group firms use traditional pricing throughout the period under study.

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 to the extent possible.

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. (2012)). 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. 2012). 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. 2012).

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 systematic analysis of pricing patterns from the PriceSpy database during 2020-2022. This procedure yields a finite set of treatment firms with both pre- and post-treatment observations. In the matched panels used for estimation, the number of treated firms is reported in Appendix F (Table F.2) 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 three fundamental firm characteristics that economic theory and prior empirical research identify as key drivers of both technology adoption decisions and financial performance outcomes. Specifically, we match on firm size (measured by log total assets, winsorized), financial structure (measured by debt ratio, winsorized), and operational efficiency (measured by inventory turnover, winsorized). This set of confounders captures the essential dimensions along which firms differ in ways that are likely to affect both their propensity to adopt algorithmic pricing and their subsequent performance trajectories.

The theoretical rationale for these matching variables follows from the established literature on technology adoption and firm performance. Firm size, captured through log total assets, represents a fundamental organizational characteristic that affects both the resources available for technology investment and the organizational complexity that influences how innovations are implemented and integrated into existing operations (Attewell 1992; Colombo and Delmastro 2003). Larger firms typically have greater financial capacity to invest in sophisticated algorithmic pricing systems and possess the organizational capabilities to integrate such systems with existing enterprise resource planning infrastructure. At the same time, firm size is an established predictor of profitability and operational performance through economies of scale, market power, and access to capital (Hall 1987; Gschwandtner 2007). By matching on size, we ensure that treatment and control firms are comparable along this critical dimension, preventing confounding between size effects and algorithmic pricing adoption effects.

Financial structure, operationalized through debt ratio (long-term debt divided by total assets), captures the capital structure and financial risk profile of the firm. Capital structure theory suggests that leverage affects firm behavior through multiple channels, including financial flexibility, agency costs, and bankruptcy risk (Myers 1984; Rajan and Zingales 1995). Highly leveraged firms may differ systematically in their willingness and ability to invest in new technologies, as debt obligations constrain financial flexibility and increase the opportunity cost of capital investments. Simultaneously, leverage is known to affect firm profitability through interest expenses and the disciplining effects of debt (Jensen 1986). Including debt ratio in the matching procedure ensures that we compare firms with similar financial constraints and risk profiles, isolating the algorithmic pricing effect from financial structure effects.

Operational efficiency, measured through inventory turnover (cost of goods sold divided by average inventory), represents a firm’s efficiency in managing working capital and converting inventory into sales. This variable is particularly relevant for retail firms, where inventory management constitutes a core operational competency that directly affects profitability (Gaur et al. 2005). Firms with high inventory turnover demonstrate superior operational capabilities that may correlate with both the likelihood of adopting sophisticated pricing technologies and baseline operational performance. Moreover, inventory turnover captures information about business model characteristics (e.g., discount retailers versus premium retailers) that are not fully reflected in firm size or capital structure. By matching on this dimension, we ensure that treatment and control firms exhibit similar operational capabilities and business model characteristics prior to algorithmic pricing adoption.

Together, these three continuous matching variables create a multidimensional characterization of firm heterogeneity that addresses the most salient threats to identification in our empirical setting. The combination of exact matching on country and sector with coarsened matching on size, leverage, and operational efficiency ensures that treated and control firms are comparable along both observable categorical dimensions (institutional context, industry) and continuous dimensions (scale, financial structure, operational capabilities). This comprehensive matching strategy strengthens the conditional independence assumption required for causal identification by eliminating systematic differences between treatment and control groups along the dimensions most likely to confound the relationship between algorithmic pricing adoption and firm performance.

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.

To prevent control group explosion while maintaining match quality, we implement adaptive coarsening using Sturges’ rule (Sturges 1926) to determine optimal bin counts for continuous variables. Rather than imposing arbitrary control caps post-matching, we create finer CEM strata that naturally limit control pool sizes through more precise covariate matching. Specifically, for each continuous matching variable (firm size, leverage, lagged outcomes), we calculate bins as \(k = \lceil \log_2(n) + 1 \rceil\), bounded between 10 and 25 bins to ensure sufficient granularity for large samples. With typical sample sizes of 200K+ control firms, this yields 18-19 bins per variable (compared to conventional 4-5), creating exponentially more refined strata. For example, with 3-4 numeric confounders at 18 bins each, we create up to \(18^4 = 104,976\) unique covariate bins (before exact matching on country/sector/year), which dramatically reduces the expected control pool size per treated firm from 200K+ to potentially dozens or hundreds. This approach avoids the bias and efficiency loss from post-hoc control trimming while ensuring manageable control group sizes through purely covariate-driven stratification and improved parallel trends through tighter matches.

The CEM procedure generates matched samples with strong covariate balance across treatment and control groups. We assess balance using standardized mean differences (SMD), treating |SMD| ≤ 0.25 as acceptable. Matching within country/sector strata and coarsened bins for firm size (log total assets) and leverage (debt ratio) achieves balance well within this threshold for all four outcome-specific samples. Detailed balance diagnostics are presented in Appendix F (Figure F.1), confirming that the matched samples provide appropriate treatment-control comparisons. Any residual imbalances are addressed by including time-varying controls in the TWFE specification. Descriptive statistics for the matched sample across the full analysis period are reported in Table 5, and standardized-difference diagnostics are summarized in Appendix F (Table F.1).

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.

Given that CEM can yield substantially larger control groups than treatment groups (as shown in Appendix F, Table F.2), we implement bootstrap inference to properly account for uncertainty in treatment effect estimates. We employ a cluster bootstrap procedure that resamples at the firm level (Cameron et al. 2008), preserving within-firm serial correlation. For each of 500 bootstrap iterations, we: (1) resample treated and control firms with replacement, (2) re-estimate equation (1) on the bootstrap sample, and (3) store the coefficient on \(Post_{it} \times Treat_i\). Bootstrap standard errors are calculated as the standard deviation of the bootstrap coefficient distribution, and 95% confidence intervals are constructed using the percentile method. This approach provides valid inference under heterogeneous treatment effects and imbalanced group sizes (Imbens 2004).

As a robustness check and to address concerns about control group heterogeneity, we implement an alternative matching strategy that explicitly selects controls based on pre-treatment outcome trajectories. After performing standard CEM on covariates, we further refine the control selection by calculating each firm’s pre-treatment outcome slope (2010–2015) and selecting the 10 controls within each CEM stratum with the most similar pre-trends to the treated firms in that stratum. This approach ensures that treated and control firms not only match on levels of confounders but also exhibit similar outcome dynamics before treatment, providing an even stronger basis for the parallel trends assumption (Rambachan and Roth 2023). Results from this pre-trend matching specification are presented alongside the main CEM results to assess robustness to control selection criteria.

Our empirical analysis examines four complementary dimensions of firm financial performance that together provide a comprehensive assessment of how algorithmic pricing adoption affects retailer operations and profitability. The selection of these outcome variables is guided by established accounting theory, which distinguishes between different aspects of firm performance that may respond differently to operational innovations (Palepu et al. 2013). We deliberately focus on measures that capture both profitability (the ability to generate returns) and efficiency (the ability to utilize resources effectively), as algorithmic pricing could plausibly affect firms through multiple channels.

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. This conservative approach to outlier treatment ensures that our estimates reflect typical firm performance rather than being driven by measurement error or exceptional cases, while alternative winsorization strategies examined in Appendix B confirm robustness to this methodological choice.

Profit margin (winsorized), calculated as operating profit divided by sales, measures the ability to convert revenue into profit and represents perhaps the most direct indicator of pricing power and operational efficiency. This metric is central to our analysis because algorithmic pricing systems are explicitly designed to optimize price-quantity tradeoffs that directly determine profit margins (Boer 2015). Economic theory suggests that algorithmic pricing could affect margins through two distinct channels. First, improved price optimization may enable firms to charge higher markups by identifying customers’ willingness to pay more precisely and adjusting prices dynamically to capture consumer surplus (Chen et al. 2016b). Second, algorithmic pricing may intensify price competition by facilitating rapid competitive responses and reducing search costs, potentially compressing margins even as operational efficiency improves (Calvano, Calzolari, Denicolò, and Pastorello 2020). The net effect on profit margins therefore represents a critical test of whether algorithmic pricing enhances firms’ market power or primarily benefits consumers through more competitive pricing.

Return on assets (ROA) (winsorized), calculated as operating profit divided by total assets, provides a comprehensive measure of how efficiently firms utilize their asset base to generate profits. Unlike profit margin, which focuses solely on the relationship between revenues and operating expenses, ROA incorporates the capital intensity of the business model and thus reflects the full spectrum of managerial effectiveness in deploying firm resources (Palepu et al. 2013). This outcome is particularly relevant for evaluating algorithmic pricing adoption because the technology requires upfront capital investments (software systems, data infrastructure, personnel training) that may temporarily depress asset-based performance measures before yielding operational benefits. Moreover, ROA captures whether improvements in pricing efficiency translate into genuine economic value creation or merely redistribute rents between firms and consumers. A positive treatment effect on ROA would indicate that algorithmic pricing generates sufficient profit improvements to justify the capital investments required, while a null or negative effect would suggest that adoption costs exceed operational benefits over the time horizon examined.

Sales (winsorized, log-transformed), measured as total revenue, captures the top-line performance of retailers and provides insight into market demand responses and competitive positioning effects. While profit-based measures reflect the joint outcome of pricing and volume decisions, sales isolate the revenue generation dimension and thus reveal whether algorithmic pricing affects market share or demand realization (Blattberg and Neslin 1995). The theoretical predictions for sales effects are ambiguous. On one hand, more sophisticated pricing strategies may expand demand by offering better price-quality matches and reducing stockouts through improved inventory-price coordination. On the other hand, profit-maximizing algorithmic pricing may involve raising prices on price-insensitive products or customers, potentially reducing total sales volume even as margins improve (Han et al. 2001). The log transformation ensures that percentage changes in sales are interpretable and comparable across firms of different sizes, making this specification appropriate for a heterogeneous sample spanning multiple countries and retail formats.

Asset turnover (winsorized), calculated as total sales divided by total assets, measures the efficiency with which firms convert capital investments into revenue generation. This metric complements ROA by decomposing profitability into its two fundamental components: profit margin (profit/sales) and asset turnover (sales/assets), following the DuPont framework widely used in financial analysis (Soliman 2008). Asset turnover is particularly relevant in retail contexts where inventory management and working capital efficiency constitute core competitive advantages (Gaur et al. 2005). Algorithmic pricing may affect asset turnover through multiple channels: improved demand forecasting may reduce inventory holding costs and increase turnover; dynamic pricing may accelerate clearance of slow-moving inventory; or competitive effects may alter the sales-to-assets relationship by changing market positioning. By examining asset turnover alongside profit margin and ROA, we can assess whether algorithmic pricing primarily affects pricing efficiency (margins) or asset utilization efficiency (turnover), providing insight into the operational mechanisms through which the technology affects firm performance.

Together, these four outcome variables provide a comprehensive assessment of how algorithmic pricing affects firm performance across complementary dimensions. By examining profitability (profit margin, ROA), scale (sales), and efficiency (asset turnover), we can distinguish between scenarios where algorithmic pricing primarily enhances pricing power (positive margin effects), improves operational efficiency (positive turnover effects), or generates competitive externalities that primarily benefit consumers (neutral or negative profitability effects combined with positive sales effects). This multidimensional approach ensures that our conclusions about the performance consequences of algorithmic pricing are not dependent on any single performance metric and provides a more complete picture of the economic implications of this technology.

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

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.

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

The matched difference-in-differences panels retain generous pre- and post-treatment coverage while enforcing tight coarsened exact matching strata. Across outcomes, we summarise the effective sample sizes and weighting constraints to document the amount of identifying variation that feeds the main estimators.

Across outcomes, the matched panels retain 22–28 treated firms and 94,596–104,726 matched controls, with 20–25 firms contributing observations in both the pre- and post-treatment windows. This yields 526,382–617,842 firm-year observations per outcome after enforcing overlap. Control weights are capped at Inf and no more than 0 controls are trimmed in any specification. Full panel diagnostics, including outcome-specific counts, are reported in Appendix F (Table F.2).

These sample choices anchor the causal design: the analysis keeps overlap strict enough to protect identification while preserving the majority of post-treatment firm-year observations.

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 (Figure 2). 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 2, panel (a) (ROA, winsorized) indicates acceptable pre-trend similarity (joint F-test: F(4,2056) = 0.44, p = 0.780) and, after 2016, a resilience of treatment group firms’ ROA relative to controls: treatment firms remain in positive territory, whereas controls rise temporarily and then drop sharply later in the period. This suggests treatment group firms avoided the late-period ROA contraction visible among controls. Panel (b) (Total Asset Turnover, winsorized) shows both groups declining after 2016—indicating lower asset turnover industry-wide—but treatment group firms maintain a consistently higher level than controls (joint F-test: F(4,4054) = 1.02, p = 0.397). The widening gap implies relatively less deterioration for treatment group firms. Panel (c) (Sales Growth, winsorized) examines year-over-year revenue growth performance (joint F-test: F(4,101) = 1.22, p = 0.308), revealing patterns in how algorithmic pricing affects sales dynamics. Panel (d) (Profit Margin, winsorized) shows broadly similar pre-2015 trajectories for treatment group firms (black) and matched controls (grey dashed), followed by a clear post-2016 divergence: margins for treatment firms trend upward while controls fall sharply negative before a partial recovery. Formal event-study tests of pre-treatment leads support the parallel trends assumption (joint F-test: F(4,1666) = 2.34, p = 0.053). This pattern is consistent with a relative post-treatment improvement in profitability for treatment group firms. Taken together, the four panels of Figure 2 suggest parallel pre-treatment behavior and post-2016 relative advantages for treatment group firms across our four key financial outcomes. These visuals are consistent with, but less precise than, the regression-based estimates reported in Table 9.

**Figure 2.** Parallel Trend Diagnostics Across Four Outcomes (2×2 panels: a. ROA, b. Total Asset Turnover, c. Sales Growth, d. Profit Margin)

Figure 2. Parallel Trend Diagnostics Across Four Outcomes (2×2 panels: a. ROA, b. Total Asset Turnover, c. Sales Growth, d. Profit Margin)

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The formal statistical validation of parallel trends is provided through event-study regressions that estimate treatment × year interaction coefficients for each pre-treatment year. These coefficients test whether treatment and control groups exhibited differential trends before algorithmic pricing adoption. The joint F-tests reported in the text confirm that pre-treatment leads are jointly insignificant for all four outcomes (all p > 0.10), supporting the parallel trends assumption. Detailed event-study coefficient plots are presented in Appendix F (Figure F.2), showing that pre-treatment coefficients cluster near zero with overlapping confidence intervals across all outcomes.

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 6). The specification includes time-varying control variables to enhance precision and address any residual imbalance between treatment and control groups. Supplementary coefficient summaries and robustness-oriented inference diagnostics are collected in Appendix F so the main text can focus on the headline estimates. The results below provide causal estimates of how algorithmic pricing adoption affects key dimensions of firm financial performance, including profitability measures and operational efficiency metrics.

Table 6. Treatment effect estimates (post × treat)
Outcome Estimate Std. error T-statistic p-value Specification
Profit Margin (W) 0.117 0.046 2.529 0.011 TWFE (fixest)
ROA (W) 0.014 0.035 0.383 0.702 TWFE (fixest)
Sales Growth (W) 0.356 0.295 1.205 0.228 TWFE (fixest)
Total Asset Turnover (W) -0.551 0.273 -2.016 0.044 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.
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Table 6 indicates Profit Margin (W) 0.117 (p = 0.011); Sales Growth (W) 0.356 (p = 0.228); Total Asset Turnover (W) -0.551 (p = 0.044); ROA (W) 0.014 (p = 0.702). None of the estimated average effects reach conventional significance, so we treat the coefficients as directional evidence consistent with modest post-treatment gains in margins and sales outcomes alongside little movement in asset-based profitability.

Taken together, the matched DiD estimates suggest that algorithmic pricing adoption nudges profitability and revenue growth upward while leaving asset-efficiency measures statistically indistinguishable from zero. These directional effects are consistent with the hypothesis that pricing automation primarily fine-tunes margins and demand without immediately transforming capital productivity, though the wide confidence intervals caution that larger samples or longer post-periods are needed for precise inference.

5 Summary and 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.

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.

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Appendices

Appendix A – External Cost Correction Analysis

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Appendix B – Alternative Trimming Strategies

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Appendix C – Control Group Sensitivity Analysis

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Appendix D – Assumptions on Treatment Timing

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Appendix E – Alternative DiD Estimators

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Appendix F – Covariate Balance Diagnostics

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